Efficacy and Safety of Fosaprepitant Dimeglumine in Preventing Chemotherapy-Induced Nausea and Vomiting (MK-0517-031): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Fosaprepitant Dimeglumine in Preventing Chemotherapy-Induced Nausea and Vomiting (MK-0517-031) (NCT01594749), a randomized phase 3 study. The primary outcome is Percentage of Participants With Complete Response From 25 to 120 Hours After Initiation of Moderately Emetogenic Chemotherapy (MEC).

2. Clinical Question

3. Trial Design

This was a phase III, randomized, double-blind, active-comparator-controlled, parallel-group study. Its stated aim was to examine whether a single 150 mg intravenous dose of fosaprepitant, given with a 5-HT3 antagonist and a corticosteroid, was superior to a regimen of a 5-HT3 antagonist and a corticosteroid without active fosaprepitant for preventing CINV associated with MEC. The registry describes in-house blinding conditions. Details of how randomization was generated, how allocation was concealed, and how masking was maintained are not reported in the registry record.

The planned treatment comparison was between the Fosaprepitant Regimen and the Control Regimen. Both included ondansetron and dexamethasone, but the listed dexamethasone doses differ: 12 mg in the fosaprepitant regimen and 20 mg in the control regimen. The control also included fosaprepitant placebo. These details matter when interpreting the contrast: the trial estimates the difference between the assigned regimens as a whole, rather than isolating the contribution of one drug under otherwise identical treatment.

The registry reports enrollment of 1015 and a completed status. The recorded study start was 2012-09-24, and the primary completion date was 2014-11-03. Arm descriptions include the Day 1 treatment details, but are truncated before all administration details are complete. The original protocol's sample-size rationale, planned interim analyses, stratification factors, and full statistical analysis plan are not reported in the registry record.

The primary outcome analysis is described for the ITT population, defined in the record as randomized participants who received at least one dose of study drug within their assigned regimen. This is not identical to an analysis of every randomized participant. The registry notes that one participant in the Fosaprepitant Regimen was excluded from the ITT population due to missing source documentation, and starts to describe an exclusion in the Control Regimen, but that description is incomplete. Further details of the analysis population and the handling of missing outcome data 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 14 participants did not receive any study drug: 4 in the Fosaprepitant Regimen and 10 in the Control Regimen. One participant who was randomized to the Control Regimen received the Fosaprepitant Regimen.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population consisted of all randomized participants who received ≥1 dose of study drug within the assigned treatment regimen. One participant in the Fosaprepitant Regimen was excluded from the ITT population due to missing source documentation. One participant in the Control Regimen was treated with fosaprepitant in error.

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: The Baseline analysis population is consistent with the Intent-to-Treat (ITT) population, i.e., all randomized participants who received ≥1 dose of study drug within the assigned treatment regimen. Note: One participant with missing source documentation in the Fosaprepitant Regimen was excluded from the ITT population.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Complete Response From 25 to 120 Hours After Initiation of Moderately Emetogenic Chemotherapy (MEC), measured over 25 to 120 hours after initiation of MEC.

The primary endpoint was the percentage of participants with complete response from 25 to 120 hours after initiation of MEC. Complete response was defined as having no vomiting and using no rescue medication during that interval. It is therefore a combined binary outcome: a participant counts as having a response only if both conditions are met. A participant who vomited or used rescue medication does not meet the stated definition.

This endpoint focuses on the period after the first 24 hours of chemotherapy, rather than the immediate period alone. It addresses whether participants remained free of vomiting and rescue medication over the specified later interval. The registry also reports complete response over the full 0 to 120 hour period and over 0 to 24 hours, as well as no vomiting over 0 to 120 hours. Those outcomes provide related but distinct views of the symptom and rescue-medication experience; they do not change the definition of the primary endpoint.

For a binary percentage outcome, the arm-level percentage describes the share of participants meeting the stated response definition. It does not measure symptom severity among participants who did not meet the definition, nor does the primary endpoint separately distinguish vomiting from rescue-medication use. Those components are combined in the complete-response measure. The registry does not report a more detailed scoring rule, adjudication process, or approach to incomplete observation during the assessment window.

Using a defined time window and a clearly stated response rule makes the treatment contrast interpretable as a comparison of the proportions meeting that rule. Interpretation still depends on how outcomes were collected and how missing observations were treated; those details are not reported in the registry record.

7. Results Posted in the Registry

• Fosaprepitant Regimen: 78.9% (396/502) versus 68.5% (341/498) on control; risk difference 10.4 percentage points (95% CI 5.0 to 15.8), risk ratio 1.15 (1.07–1.24); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Participants With Complete Response From 0 to 120 Hours After Initiation of MEC

• 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:
  • Fosaprepitant Regimen: 77.1% (387/502) versus 66.9% (333/498) on control; risk difference 10.2 percentage points (95% CI 4.7 to 15.8), risk ratio 1.15 (1.07–1.25); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Fosaprepitant Regimen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Complete Response From 0 to 24 Hours After Initiation of MEC

• 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:
  • Fosaprepitant Regimen: 93.2% (468/502) versus 91.0% (453/498) on control; risk difference 2.3 percentage points (95% CI -1.1 to 5.6), risk ratio 1.02 (0.99–1.06); unadjusted two-proportion z-test p = 0.185.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fosaprepitant Regimen and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With No Vomiting From 0 to 120 Hours After Initiation of MEC

• 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:
  • Fosaprepitant Regimen: 82.7% (415/502) versus 72.9% (363/498) on control; risk difference 9.8 percentage points (95% CI 4.7 to 14.9), risk ratio 1.13 (1.06–1.21); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Fosaprepitant Regimen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes give a broadly consistent directional pattern for complete response over the longer observation period and for remaining free of vomiting over the full period. The early complete-response outcome is less conclusive: its posted comparison does not provide clear statistical evidence of a difference under conventional interpretation. This pattern is compatible with the primary result being associated with the later assessment period, but it should not be taken as proof that treatment effects truly differ by time window.

Each secondary measure differs in its definition or time interval. Complete response requires both no vomiting and no rescue medication, while the no-vomiting outcome does not include rescue-medication use in its stated definition. The assessment windows also differ. These outcomes can help describe whether the primary pattern is accompanied by related endpoint patterns, but they are not interchangeable replications of the primary endpoint.

The registry reports three secondary outcomes, while the outcome record lists six measures and five analyses overall. The reason that only three secondary outcomes are posted in the summary is not reported in the registry record. Nor does the record report a prespecified hierarchy, multiplicity adjustment, or confirmatory status for the secondary analyses.

Unadjusted secondary p-values carry less weight when several outcomes or time windows are examined. General statistical context: testing multiple hypotheses increases the chance of at least one apparently unusual result even when none of the underlying effects is real. Adjustment procedures or a prespecified testing sequence can address this issue, but the registry does not report whether either was used for these secondary endpoints. The secondary findings are therefore best treated as supporting descriptive evidence, not as independent confirmation of the primary result.

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

• Percentage of Participants With Complete Response From 0 to 120 Hours After Initiation of MEC
• Percentage of Participants With Complete Response From 0 to 24 Hours After Initiation of MEC
• Percentage of Participants With No Vomiting From 0 to 120 Hours After Initiation of MEC

9. Statistical Interpretation

10. Statistical Methods Explained

What does a binary percentage represent?

The primary outcome is binary at the participant level: each person either meets the complete-response definition for the specified period or does not. The reported percentage is the proportion meeting that definition in each treatment group. It is a group summary, not an estimate of how often vomiting occurred among those who experienced it, and not a measure of symptom intensity.

General statistical context: a proportion is estimated from a finite group of observations, so it is subject to sampling variability. A comparison of two proportions can be expressed as an absolute risk difference, a risk ratio, or an odds ratio. These measures answer different questions. An absolute difference compares the proportions directly; a risk ratio compares them multiplicatively; an odds ratio compares the odds of response. The primary recalculation uses the risk difference, which keeps the contrast on the scale of percentage-point change when interpreted in percentage terms. The reported ratio measures are alternative summaries, not additional outcomes.

How should the absolute risk difference be read?

The recalculated risk difference is 0.104, with an interval from 0.050 to 0.158. A positive estimate means the observed response proportion is higher in the Fosaprepitant Regimen than in the Control Regimen. The interval gives a range of values compatible with the observed data under the interval method's assumptions. It conveys uncertainty about the size of the contrast, rather than certainty that the true effect equals the point estimate.

General statistical context: an interval is not a range containing a fixed proportion of individual participants, and it does not account automatically for every possible source of bias or uncertainty. Its interpretation relies on the analysis method and its assumptions. The registry record does not identify the confidence level for the recalculated intervals, so it should not be inferred from the displayed numbers.

What does the p-value add?

The unadjusted recalculation reports p <0.001 for the primary comparison, and the registry's Cochran-Mantel-Haenszel analysis also reports p <0.001. A p-value assesses how unusual data at least as incompatible with a null comparison would be if that null model and the test assumptions held. It is not the probability that the treatments are equivalent, and it does not state the probability that the observed difference arose by chance in a general sense.

A small p-value alone does not establish whether a difference is clinically important. The size of the observed contrast and its precision are also relevant, as are endpoint meaning and the design. Conversely, a p-value above a conventional threshold is not proof of no effect. This is particularly important for the secondary endpoint covering 0 to 24 hours, where the registry and unadjusted recalculation report different p-values that are both above 0.05.

Why distinguish the recalculation from the sponsor analysis?

The recalculated comparison is a simple, unadjusted analysis based on the posted counts and group sizes. The registry reports a Cochran-Mantel-Haenszel analysis for the primary comparison. General statistical context: this method can combine information across strata, producing an adjusted comparison when a study has been analyzed within defined strata. The registry does not report the strata or enough detail to reconstruct that analysis. Thus, the recalculated risk difference and interval are useful summaries of the marginal posted data, but they are not a reproduction of the sponsor's full analysis.

The registry reports a sponsor p-value of <0.001 for the primary result, matching the threshold shown by the unadjusted recalculation. The posted record indicates no discrepancy for this outcome. Agreement in the reported p-value threshold does not make the methods identical: the sponsor's result comes from its stated method, while the recalculation uses the displayed summary statistics.

What does the design contribute to interpretation?

Random assignment is intended to make the treatment groups comparable, on average, with respect to measured and unmeasured factors at the time of assignment. Double masking is intended to reduce the influence of treatment knowledge on care, reporting, and assessment. These are general design principles, not guarantees that bias is absent. The registry identifies the trial as randomized and double-blind but does not report the sequence-generation procedure, concealment details, or masking assessment.

The parallel-group structure means participants were assigned to one regimen rather than crossing between regimens. The active comparison evaluates the two full regimens. Because the listed dexamethasone doses differ, the observed contrast cannot be interpreted as the isolated effect of adding fosaprepitant while holding every other medication dose constant. The trial's stated question concerns the regimen comparison.

The sponsor's stated analysis population is the ITT population, with the registry defining it as randomized participants who received at least one dose of study drug in the assigned regimen. That definition excludes randomized participants who received no dose, and the record also describes exclusions within the population. The exact handling of missing primary outcomes and the full analysis plan are not reported in the registry record. These details matter because analysis populations and missing-data rules can affect estimates and uncertainty.

11. Confidence Intervals and Precision

The primary recalculated absolute risk difference is 0.104, with an interval from 0.050 to 0.158. The interval lies on the positive side of zero, consistent with the observed response proportion being higher in the Fosaprepitant Regimen. Its width indicates that the point estimate should not be read as exact; the data are compatible with a range of positive differences under the recalculation's assumptions. The registry record does not state the confidence level for this recalculated interval, so a confidence percentage should not be attached to it.

Precision is affected by the amount of information in the comparison and by the variability inherent in a binary outcome. General statistical context: larger groups often yield more precise estimates when other features are similar, but precision is not the same as freedom from bias. An interval based on posted counts cannot resolve uncertainty about outcome collection, missing observations, or applicability beyond the trial setting.

The group percentages are 78.9% and 68.5%. Those rounded arm-level values are descriptive summaries; the recalculated comparison uses the posted event counts and denominators. Small differences between calculations from rounded percentages and calculations from counts can arise because the percentages are rounded. No new estimate should be inferred by subtracting the displayed rounded percentages.

The sponsor's primary p-value, p <0.001, is from the Cochran-Mantel-Haenszel analysis. The recalculated interval and risk difference are unadjusted summaries and do not supply the sponsor method's adjusted interval. The registry record does not report an estimate or interval from the sponsor analysis, so the two uncertainty summaries cannot be compared directly.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design rationale. For these binary outcomes, the figures are participants per arm, not a total across arms and not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustration uses the stated fraction of the observed effect as the effect to detect. The original sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm in a hypothetical design that would have an 80% probability of detecting the specified effect under the listed assumptions, if that effect were the true one and the statistical model applied. The 90% power column uses a higher target probability of detecting that same specified effect. These are design targets, not descriptions of the trial's observed results.

Rows for 100% of the observed effect use the full observed contrast as the planning target. Rows for 75% and 50% of the observed effect use progressively smaller target effects. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the target effect decreases. This relationship is a general planning principle, not a claim about what the original investigators assumed.

These figures are not observed power. They do not calculate the probability that the completed trial detected its own observed result, and they should not be used to reinterpret the trial's p-value. They are hypothetical planning estimates tied to an effect size estimated from these data. Since the observed effect itself is uncertain, the planning figures are also illustrative rather than a guarantee that a future study with those group sizes will achieve a particular result.

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 = 0.685; treatment proportion p₁ = 0.789; average p̄ = 0.737.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6228 = 1.2206.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6184 = 0.5205.
4. n = (1.2206 + 0.5205)² / (0.1041)² = 279.7, rounded up to 280 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 <- 0.684738955823293                          # control proportion
p1 <- 0.788844621513944                          # 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(1594749)
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 = 280 (80% power), 374 (90% power)
 75% of observed effect: n per arm = 514 (80% power), 688 (90% power)
 50% of observed effect: n per arm = 1,190 (80% power), 1,593 (90% power)
power.prop.test: 279.7 
Simulated power at n = 280 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a Cochran-Mantel-Haenszel analysis for the primary comparison, with p <0.001. The unadjusted recalculation from the posted counts also gives p <0.001. The registry record indicates no discrepancy for this endpoint, so the broad conclusion from the two reported p-value thresholds is consistent.

The recalculation is not the sponsor's analysis reproduced from its individual-level data. It uses posted summary counts and group sizes to estimate an unadjusted risk difference and interval. The Cochran-Mantel-Haenszel method may account for stratification, but the registry does not identify the strata or provide the details needed to reconstruct the analysis. The posted record also does not give the sponsor's effect estimate or interval for this endpoint.

Accordingly, the sponsor analysis should be read as the trial's reported inferential result, while the unadjusted calculation is a transparent summary derived from the posted group data. They answer closely related questions but need not have identical estimates or uncertainty. The matching p-value threshold does not establish that the procedures are interchangeable.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and five analyses, including the primary outcome and three posted secondary outcomes. It does not report how many outcomes were prespecified for formal testing, whether the secondary outcomes were exploratory or confirmatory, or whether a multiplicity procedure was used. It also does not report a hierarchy or gatekeeping sequence for interpreting tests.

General statistical context: when several hypotheses are tested, the chance of at least one small p-value under a collection of null effects can increase. A prespecified testing strategy can help control the overall false-positive risk, while exploratory analyses can be useful for generating further questions. Without the analysis plan, it is not possible to determine how the trial addressed multiplicity. The secondary p-values should therefore not be interpreted as if each were necessarily an isolated confirmatory test.

The registry defines the primary analysis population as randomized participants who received at least one dose of study drug within the assigned regimen. It notes that one Fosaprepitant Regimen participant was excluded from that population due to missing source documentation. The description then begins to note an exclusion in the Control Regimen but is truncated; the reason and remaining detail are not reported in the registry record.

The registry does not report how missing primary outcome data were handled, whether any imputation was used, or how participants without evaluable assessments were treated in the analyses. It also does not report a sensitivity analysis examining alternative assumptions about missingness. Missing-data methods can affect a binary percentage comparison if outcome availability differs or is related to response, so these omissions limit independent assessment of robustness.

The sponsor's reported primary method is Cochran-Mantel-Haenszel, but the record does not report the strata used, the handling of missing data within that method, or a complete statistical analysis plan. These details should not be inferred. The reported method and population definition provide some information, but they do not fully specify the analysis.

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 (1.6%), neutropenia (0.8%), pneumonia (0.6%), asthenia (0.4%), diverticulitis (0.4%).

For serious adverse events, the registry reports affected participants and those at risk separately by regimen: 39 of 504 in the Fosaprepitant Regimen and 35 of 497 in the Control Regimen. For other adverse events, the corresponding figures are 190 of 504 and 193 of 497. These are descriptive counts with their recorded denominators; they are not adjusted comparisons and do not establish that one regimen caused more or fewer events.

The listed serious adverse event terms include febrile neutropenia at 1.6%, neutropenia at 0.8%, pneumonia at 0.6%, asthenia at 0.4%, diverticulitis at 0.4%, and back pain at 0.4%. The registry summary does not give further context for these terms in the listed data, such as event timing, severity beyond the serious classification, or a comparative analysis for each term. The percentages should therefore be read as reported descriptive values, not as treatment effects.

Deaths are not reported in the registry record. The safety figures alone do not determine causality, relative safety, or the overall balance of benefits and harms. Such judgments require fuller clinical and safety context than these aggregate counts provide.

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

The central statistical finding is that the posted percentage meeting the complete-response definition from 25 to 120 hours was higher in the Fosaprepitant Regimen than in the Control Regimen. The unadjusted difference is estimated with an interval that remains on the positive side of zero, and the registry's own primary analysis reports p <0.001. This describes the observed comparison under the study's endpoint definition and analysis population.

It does not mean that every participant in the fosaprepitant group had complete response, or that no participant in the control group did. Nor does it show which component of the combined endpoint accounts for the group contrast. Complete response requires both no vomiting and no rescue medication, so the primary measure cannot separate those components.

The result also does not isolate the effect of fosaprepitant from all other aspects of the regimen. The listed dexamethasone dose differs between treatment groups, and the comparison is between complete assigned regimens. The trial was designed to compare those regimens in the setting of MEC; interpretation should remain within that scope.

A statistically strong comparison is not a direct measure of clinical importance. The registry does not report a threshold for a clinically meaningful difference, and the estimate should be considered alongside the interval, endpoint definition, and limitations of the record. The result does not guarantee the same response pattern in other chemotherapy contexts, populations, or care settings.

Finally, the public registry summary does not provide the full statistical analysis plan, missing-data procedures, or multiplicity strategy. Those gaps do not erase the reported result, but they constrain how completely it can be independently evaluated. The evidence describes an observed regimen contrast; it is not a personalized prediction or treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why the definition and timing of an endpoint matter. Complete response is not simply a count of vomiting episodes: it requires both no vomiting and no rescue medication during a specified window. The primary window begins after the first 24 hours and continues through 120 hours after MEC initiation. A reader comparing outcomes needs to keep both the composite definition and the time interval in view.

It also demonstrates the value of reporting an absolute contrast alongside group percentages. Percentages describe each arm separately, while the risk difference directly expresses the contrast between groups on an absolute scale. An interval adds information about the uncertainty around that estimate. A p-value alone would not show the size or precision of the observed difference.

The trial's active-comparator design raises an important estimand question: what was actually compared? The assigned regimens differ not only in active fosaprepitant versus placebo but also in the listed dexamethasone dose. The result therefore pertains to the regimen comparison, not to an isolated drug effect under identical co-treatment.

The difference between a sponsor analysis and a simple recalculation is another useful statistical lesson. The posted counts support an unadjusted comparison, whereas the registry names a Cochran-Mantel-Haenszel method for its own test. Similar p-value thresholds do not make the methods identical, and an unadjusted summary cannot recreate an analysis based on details not reported in the record.

Finally, the secondary outcomes show why multiple testing plans matter. Results across related outcomes can add context, but they should not be treated as several independent confirmations when the analysis plan and multiplicity handling are not reported. Reading the primary result together with the endpoint definitions, uncertainty, and limits of the registry record gives a more careful account than relying on a single significance label.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves important design and analysis details unavailable. It does not report the original sample-size justification, randomization procedure, allocation-concealment method, masking assessment, interim-analysis plan, full statistical analysis plan, or any stratification factors used in the Cochran-Mantel-Haenszel analysis. Those omissions make it difficult to reconstruct the sponsor's analysis or assess every planned decision from the registry summary alone.

The primary population description is incomplete. It defines the ITT population as randomized participants who received at least one dose, then notes exclusions, including one Fosaprepitant Regimen participant excluded for missing source documentation. The control-regimen description is cut off. Missing-outcome handling and sensitivity analyses are not reported in the registry record, limiting assessment of how incomplete follow-up might affect the comparison.

The registry lists three secondary outcomes but also records six outcome measures and five analyses. It does not explain the difference or report a multiplicity strategy. Secondary findings therefore have uncertain confirmatory status, and their p-values should be interpreted cautiously.

The treatment contrast is between regimens, with different listed dexamethasone doses. It cannot be read as a clean estimate of fosaprepitant's isolated contribution. In addition, the endpoint is a composite response measure and the public summary does not provide separate primary comparisons for vomiting and rescue-medication use. The result is specific to the described MEC setting; the registry record does not establish how well it generalizes to other contexts.

Safety reporting is also limited to aggregate counts and a short list of serious event terms. The record does not provide detailed timing, event-level attribution, or a complete comparative safety analysis in the registry record. Deaths are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Fosaprepitant Dimeglumine in Preventing Chemotherapy-Induced Nausea and Vomiting (MK-0517-031) — NCT01594749.
• Registry record last updated 2018-09-04; status last verified 2018-08.
• Results first posted 2015-09-25.
• 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

NCT01594749 is a completed phase III randomized, double-blind, parallel-group study of fosaprepitant-containing and control regimens for prevention of CINV associated with MEC. The registry reports enrollment of 1015. The primary endpoint was complete response from 25 to 120 hours after MEC began, defined as no vomiting and no use of rescue medication.

The posted primary percentages were 78.9% for the Fosaprepitant Regimen and 68.5% for the Control Regimen. The unadjusted recalculation gives a risk difference of 0.104, with an interval from 0.050 to 0.158 and p <0.001. The sponsor's Cochran-Mantel-Haenszel analysis also reports p <0.001.

Interpretation is limited by incomplete public details about the original design assumptions, missing-data handling, multiplicity, and the full statistical analysis plan. The observed comparison concerns the assigned regimens and the stated endpoint, not an isolated drug effect or a guarantee of results in other settings.