A Study to Assess the Bioequivalence of Aprepitant and Fosaprepitant and the Effect of Food on Aprepitant Bioavailability (0869-165): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Bioequivalence of Aprepitant and Fosaprepitant and the Effect of Food on Aprepitant Bioavailability (0869-165) (NCT00945321), a randomized phase 1 study. The primary outcome is Area Under the Curve (AUC(0 to Infinity)) Following Single Dose Administration of Aprepitant 165 mg or 185 mg and Fosaprepitant 150 mg.

2. Clinical Question

The study was completed, with enrollment of 42. Its focus was bioequivalence and food effect after single-dose administration. The registry record does not report a patient-outcome question such as whether one regimen better controls chemotherapy-related symptoms. Its results therefore address drug exposure under the studied conditions, and their interpretation depends on the pharmacokinetic analyses and comparison criteria used.

3. Trial Design

The registry record describes a randomized, open-label Phase 1 crossover study of a single dose of aprepitant and a single intravenous infusion of fosaprepitant dimeglumine in healthy young adult subjects. Enrollment was 42. The study began in 2009-02, reached primary completion in 2009-03, and is listed as completed. No masking was used.

The interventions included aprepitant 165 mg, aprepitant 185 mg, fosaprepitant 150 mg and aprepitant with food. The primary outcome compared the area under the curve from zero to infinity after aprepitant 165 mg or 185 mg and fosaprepitant 150 mg. The stated measurement period was through 72 hours postdose. Food-effect results separately distinguish light and high-fat food conditions for the two aprepitant doses.

A crossover design means participants receive treatment conditions across study periods, rather than each participant being assigned only to one parallel treatment group. General explanation: this structure can support within-participant comparisons, but it also makes period order, carryover and the analysis of repeated observations relevant. The registry record does not report treatment sequence details, washout duration, or how period and sequence effects were handled.

The pharmacokinetic analysis included all subjects except one who dropped out after Period 1 due to accidental overdose. Posted endpoint counts vary by treatment condition: the fasted comparisons include 41, while food-condition groups have smaller counts. The record does not explain the reasons for each food-condition count or provide a participant-flow account beyond the stated dropout. The detailed protocol, original sample-size justification and full statistical 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.

Period 1

Reasons for not completing this period:

Period 2

Period 3

Period 4

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All subjects excluding one subject who dropped from the study after Period 1 due to accidental overdose were included in the pharmacokinetic (PK) analysis.

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 Area Under the Curve (AUC(0 to Infinity)) Following Single Dose Administration of Aprepitant 165 mg or 185 mg and Fosaprepitant 150 mg, measured over Through 72 Hours Postdose.

The primary endpoint is area under the concentration-time curve from zero to infinity after a single dose, reported in ng•hr/mL. AUC represents drug exposure over time: it aggregates measured concentration across the postdose period and estimates exposure extending to infinity. The registry states that measurements were followed through 72 hours postdose. The endpoint is recorded as a mean with standard deviation.

In a bioequivalence study, exposure measures such as AUC are used to compare the extent of drug availability after different formulations or routes of administration. The registry’s posted sponsor analyses express comparisons as least-squares mean ratios. A ratio places the estimated exposure in one treatment condition relative to another, which is a common way to assess whether exposure is similar within prespecified bounds. The bioequivalence margins and the precise decision criterion are not reported in the registry record, so the reported ratios and intervals should be read as estimates rather than as a standalone declaration of equivalence.

The food comparisons use the same exposure concept to describe how aprepitant exposure varies under fed conditions. This endpoint is pharmacokinetic, not a direct clinical outcome. It does not measure symptom relief, treatment response or patient experience. The use of AUC is appropriate to the study’s stated questions about bioavailability and exposure, but it answers those questions only within the studied dosing conditions and population.

7. Results Posted in the Registry

• 185 mg Aprepitant (Fasted State): mean 39,053 versus 34,589 on control; difference 4,464 (95% CI 4,447 to 4,481), standardized effect d = 115.60; z-test p = <0.001.
• 150 mg Fosaprepitant Dimeglumine (Fasted State): mean 37,375 versus 34,589 on control; difference 2,786 (95% CI 2,769 to 2,803), standardized effect d = 70.35; z-test p = <0.001.
• 165 mg Aprepitant (High-Fat): mean 50,172 versus 34,589 on control; difference 15,583 (95% CI 15,566 to 15,600), standardized effect d = 425.61; z-test p = <0.001.
• 185 mg Aprepitant (High-Fat): mean 60,578 versus 34,589 on control; difference 25,989 (95% CI 25,953 to 26,025), standardized effect d = 592.79; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

General explanation: a continuous endpoint is measured on a numeric scale, rather than counted as a yes-or-no event. Here, the endpoint is AUC in ng•hr/mL, and the registry reports means and standard deviations for the treatment groups. A mean describes the central level of the measurements. A standard deviation describes their spread around the mean; it is not the same thing as a confidence interval for the mean or treatment contrast.

What does the crossover design imply?

General explanation: in a crossover study, each participant may receive more than one treatment condition over separate periods. This can make within-participant comparisons informative because each participant can serve as their own reference. It also means that analysis should account for the repeated measurements and the order in which conditions are received. Period effects, sequence effects and carryover can matter. The registry record identifies a crossover design, but treatment sequences, washout, and the statistical handling of these features are not reported in the registry record. It is therefore not possible to assess those design details from the posted record alone.

What are the sponsor’s reported comparisons?

The posted sponsor results use least-squares mean ratios. General explanation: a least-squares mean is an estimate derived from a statistical model, potentially adjusted for features included in that model. A ratio expresses one estimated mean relative to another. A value of 1 would indicate equal estimated means on the ratio scale, while values on either side indicate the direction and size of the relative estimate. The precise model specification and adjustment variables are not reported in the registry record.

For the two fasted comparisons, the registry reports two one-sided tests. General explanation: this is a testing approach often used for equivalence questions. Instead of testing whether treatments differ in either direction, the two tests assess whether the contrast lies within lower and upper equivalence limits. The limits are essential to interpreting the result. Those margins are not reported in the registry record, so the posted p-values cannot be judged against the intended equivalence boundaries. A p-value is not the probability that the null hypothesis is true, and it does not by itself establish equivalence.

The food comparisons report 90% confidence intervals, while the fasted sponsor comparisons report 95% confidence intervals. General explanation: a confidence interval gives a range of values compatible with the data and the analysis under repeated-sampling assumptions. Its width reflects precision: narrower intervals indicate less statistical uncertainty than wider intervals, for the specified analysis. An interval should be read alongside the estimate and the analysis purpose; it does not show the range of individual participants’ values.

How do the recalculations differ?

The recalculated comparisons are unadjusted mean differences based on the posted summary statistics. They report differences between group means, confidence intervals, and unadjusted p-values. General explanation: an unadjusted comparison uses the summaries without a model that accounts for crossover structure or other covariates. It is therefore not a substitute for the sponsor’s model-based analysis. The sponsor reports ratios, while the recalculations report differences, so the two approaches estimate contrasts on different scales. The registry record does not identify a discrepancy, but the sponsor’s stated analysis is the more relevant result for the bioequivalence question.

The recalculated p-values are unadjusted. General explanation: when multiple comparisons are made, testing each one separately can increase the chance of at least one small p-value arising by chance across the collection of tests. A multiplicity adjustment or a prespecified testing hierarchy can address this issue, but the registry record does not report whether or how such procedures were planned. The posted p-values should therefore be interpreted as individual comparison results, not as evidence that multiplicity has been addressed.

Finally, the registry provides limited analysis-population information. It identifies the pharmacokinetic population and one exclusion after a dropout, but the detailed missing-data approach and analysis plan are not reported in the registry record. General explanation: missing observations can affect a comparison if the reasons for missingness are related to treatment or outcome. The available counts and description are not enough to assess that possibility in detail.

10. Confidence Intervals and Precision

The sponsor’s fasted comparisons have 95% confidence intervals for least-squares mean ratios. For aprepitant 165 mg versus fosaprepitant 150 mg, the estimate is 0.93 and the interval is 0.84 to 1.02. For aprepitant 185 mg versus fosaprepitant 150 mg, the estimate is 1.05 and the interval is 0.96 to 1.15. These intervals show the range of values compatible with each reported model-based comparison under its assumptions. Whether either interval meets the study’s equivalence criterion cannot be determined because the equivalence margins are not reported in the registry record.

The food-effect estimates have 90% confidence intervals: 1.47 (1.23 to 1.76) for 165 mg with high-fat food, 1.08 (0.88 to 1.32) for 165 mg with light food, 1.22 (1.01 to 1.46) for 185 mg with high-fat food, and 1.43 (1.16 to 1.75) for 185 mg with light food. The intervals vary in width, and the underlying food-condition counts are smaller than the fasted counts. This gives context for the precision of these estimates; it does not establish why the counts differ.

The recalculated mean-difference intervals are separate unadjusted results and should not be combined with the sponsor’s ratio intervals. General explanation: confidence intervals express uncertainty in an estimate, not certainty about an individual response or a clinical outcome. They also depend on the analysis model and its assumptions. Here, the registry does not report enough detail about model specification, crossover handling or equivalence bounds to independently assess the full precision framework.

11. 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 80% power and participants per arm for 90% power. They are not total event counts: the endpoint is continuous, and the planning display is expressed per arm. For every listed comparison and effect fraction, the posted values are 1 participant per arm for 80% power and 1 participant per arm for 90% power. Those figures are planning illustrations based on the observed effect, not the original trial’s design calculation.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The 80% power column describes the planned chance of detecting an effect of that size under those assumptions if the effect were present. The 90% power column describes a higher target chance of detection under the same stated framework. Neither is a probability that the treatment effect is true.

Smaller effects need more participants to distinguish them from random variation at a given power target. The displayed figures do not change across the listed fractions, so they should be read cautiously as rough illustrations rather than as a usable design recommendation. The original sample-size justification and design assumptions are not reported in the registry record. These are planning calculations, not observed power; observed power is not a useful substitute for interpreting the estimates and confidence intervals from the completed study.

12. 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 4464.000; pooled standard deviation σ = 38.616.
2. n = 2 × (1.96 + 0.842)² × 38.616² / 4464.000² = 0.0, rounded up to 1 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
delta <- 4464                      # observed difference in means
sigma <- 38.6156703942842                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(945321)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1 (80% power), 1 (90% power)
 75% of observed effect: n per arm = 1 (80% power), 1 (90% power)
 50% of observed effect: n per arm = 1 (80% power), 1 (90% power)
power.t.test: 1.3 
Simulated power at n = 1 per arm: NA (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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.

13. Analyses Reported by the Sponsor

The registry’s own reported analyses are least-squares mean ratios for the fasted and food comparisons. Those results should be kept distinct from the recalculated unadjusted mean differences. The sponsor’s analyses use a ratio scale and, for the fasted comparisons, are identified as two one-sided tests. The recalculations use the posted summary statistics to estimate differences between means. Because the estimands and scales differ, the recalculated estimates and p-values do not reproduce the sponsor’s analysis.

The record does not flag a discrepancy between the reported and recalculated results. Even so, the sponsor’s analysis is the relevant posted analysis for the stated bioequivalence comparisons. The registry record does not report the equivalence margins or enough model detail to independently verify the sponsor’s decision criteria. The recalculations should therefore be treated as descriptive, unadjusted checks rather than as replacements for the sponsor’s results or proof that a bioequivalence criterion was met.

14. Multiplicity, Missing Data and Analysis Populations

The record posts two primary fasted bioequivalence comparisons and four food-condition comparisons. It does not report a multiplicity adjustment, a testing hierarchy, or whether any comparisons were considered exploratory. General explanation: when several hypotheses are tested, interpreting each p-value as if it were the only test can understate the overall chance of a false-positive finding. A prespecified strategy can clarify which comparisons are confirmatory and how error across them is handled. That strategy is not reported in the registry record. The food comparisons have no posted p-values, but they do have estimates and confidence intervals.

The registry identifies a pharmacokinetic analysis population that excluded one subject who dropped after Period 1 due to accidental overdose. It does not report a fuller account of missing observations, reasons for the different counts in food conditions, or the method used to handle missing data. General explanation: missing data can affect estimates when the chance of an observation being absent is associated with treatment condition or the outcome. The available information does not establish whether such bias occurred.

The analysis population is described as all subjects except the one stated exclusion, but a more detailed definition of analysis sets is not reported in the registry record. It is also not reported whether the sponsor conducted sensitivity analyses using alternative populations or missing-data assumptions. In crossover studies, the handling of participants who do not complete every period can be consequential, and the posted record does not provide enough information to evaluate that handling.

The record also does not report the detailed statistical model, covariates, treatment-sequence handling, or period-effect methods. These omissions limit independent assessment of the sponsor’s inference. The posted results can be described as reported, but the registry record does not support reconstruction of the full analysis plan.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: accidental overdose (2.4%).

The adverse-event record lists serious events by treatment group and number at risk. For 165 mg aprepitant, 0 of 41 participants had a serious adverse event reported; for 185 mg aprepitant, 1 of 42 did. For fosaprepitant 150 mg, 0 of 41 did. In the fed groups, the record reports 0 of 21 for 165 mg aprepitant and 0 of 20 for 185 mg aprepitant. The registry also lists Accidental Overdose as a serious-event term at 2.4%.

These figures describe the posted event counts and denominators; they are not estimates of comparative safety. The record does not report deaths as a numeric value, so deaths are not reported in the registry record. Because the trial used a crossover design and the adverse-event groups may reflect treatment exposures across periods, the counts should not be added across groups to infer a number of unique affected participants. The registry record does not provide enough detail to assess event timing, relatedness, or severity beyond the serious-event classification.

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

The results address pharmacokinetic exposure after single-dose administration in healthy young adult subjects. The AUC estimates describe drug exposure through the measured postdose period and the sponsor’s ratios describe relative exposure between treatment conditions. The study does not report clinical outcomes such as nausea control, vomiting, chemotherapy completion or quality of life. Its results therefore cannot establish comparative clinical benefit in people receiving chemotherapy.

The fasted sponsor analyses report ratios and confidence intervals for comparisons of aprepitant with fosaprepitant. They are identified as two one-sided tests, but the equivalence margins are not reported in the registry record. A conclusion about whether the study met its equivalence criterion cannot be independently made from the posted estimates alone. The food comparisons report estimates and 90% confidence intervals, which describe relative exposure under the listed food conditions; they do not by themselves establish clinical importance.

The study enrolled 42 and was conducted in a crossover design. The pharmacokinetic population excluded one participant after a dropout following accidental overdose, and the food-condition analyses have smaller counts than the fasted analyses. These features and the missing information about model details and treatment sequence constrain how far the estimates can be generalized. General explanation: a pharmacokinetic result in healthy volunteers may inform understanding of exposure, but it is not itself evidence of a clinical effect in a different population or setting.

The registry record also provides limited safety detail. The serious-event counts are small and do not constitute a comprehensive comparison of harms. Overall, the posted data support a description of exposure estimates under the conditions studied, with uncertainty reflected in the reported intervals. They do not establish that one treatment is clinically superior, nor do they answer a patient-outcome question.

17. Why This Trial Matters Statistically

This trial is statistically useful because it illustrates how a bioequivalence question differs from a simple test of whether two means are equal. The sponsor reports least-squares mean ratios and identifies two one-sided tests for the fasted comparisons. Equivalence depends on whether the estimate is sufficiently precise to fall within prespecified bounds, so the margins are central to interpretation. Those margins are not reported in the registry record.

The study also illustrates the importance of keeping analysis scales distinct. A ratio is a relative comparison, while a mean difference is an absolute comparison on the endpoint’s measurement scale. The unadjusted recalculations and sponsor analyses therefore do not answer the question in identical ways. Treating their estimates as interchangeable would obscure both the estimand and the role of the statistical model.

The crossover structure makes within-participant analysis relevant, but the registry record does not describe treatment sequence, washout or handling of period effects. That is a reminder that a design label alone is not enough to reproduce or fully audit an analysis. Counts also vary across conditions, and only limited information about missingness is posted.

Finally, this study separates pharmacokinetic evidence from clinical outcomes. AUC is suited to comparing exposure, but the endpoint is not a measure of symptom control or patient benefit. Statistical interpretation must stay aligned with the question the endpoint can answer.

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.

The registry record leaves several trial-specific uncertainties. It does not report the equivalence margins, so the two one-sided tests and their p-values cannot be checked against the decision boundaries. The sponsor’s model specification, adjustment variables and handling of treatment sequence and period effects are also not reported in the registry record. These details matter for interpreting results from a crossover design.

The participant counts differ across treatment conditions. The record states that one participant dropped after Period 1 due to accidental overdose and was excluded from the pharmacokinetic analysis, but it does not account for the smaller counts in the food comparisons. Nor does it describe missing-data handling or sensitivity analyses. This limits assessment of whether the available observations represent the intended treatment comparisons.

The study was conducted in healthy young adult subjects and used single-dose administration. Its pharmacokinetic results do not directly answer questions about clinical outcomes or use in patients receiving chemotherapy. The safety information is limited to posted event counts, with no numeric death count and little detail on timing or relatedness.

Additional limitations include the absence of reported multiplicity procedures and the lack of a detailed original sample-size justification. The planning illustrations based on observed effects are not a substitute for the trial’s original design assumptions. These limits do not negate the posted estimates, but they restrict independent evaluation and the scope of conclusions that can be drawn from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Assess the Bioequivalence of Aprepitant and Fosaprepitant and the Effect of Food on Aprepitant Bioavailability (0869-165) — NCT00945321.
• Registry record last updated 2015-01-28; status last verified 2015-01.
• Results first posted 2010-06-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

This completed randomized, open-label Phase 1 crossover study enrolled 42 healthy young adult subjects. It assessed single-dose aprepitant and fosaprepitant exposure, including comparisons by dose and food condition. The primary endpoint was AUC from zero to infinity, measured through 72 hours postdose.

The registry reports mean exposure summaries and sponsor analyses using least-squares mean ratios. Fasted comparisons are identified as two one-sided tests; food comparisons include 90% confidence intervals. Equivalence margins, detailed model specifications and the original sample-size justification are not reported in the registry record.

The results characterize pharmacokinetic exposure in the studied conditions, not clinical outcomes. The record reports one exclusion from the pharmacokinetic analysis after a dropout following accidental overdose and provides limited adverse-event information.