Dose-finding Study of APD403 to Prevent Nausea and Vomiting After Chemotherapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose-finding Study of APD403 to Prevent Nausea and Vomiting After Chemotherapy (NCT01857232), a randomized phase 2 study. The primary outcome is Number of Participants With Delayed Phase Complete Response(CR).

2. Clinical Question

The trial record identifies a randomized, double-blind, dose-finding Phase II study. The clinical question is about a defined response during a particular post-chemotherapy window, rather than nausea alone or symptoms over the entire period after treatment. The overall-phase response is posted as a secondary outcome and uses a longer timeframe, from 0 to 120 hours.

3. Trial Design

The registry classifies this as a randomized, parallel-group, quadruple-masked Phase II study. Enrollment was 342, and the status is COMPLETED. The study title identifies cisplatin- or anthracycline/cyclophosphamide (AC)-based chemotherapy as the treatment setting. Its stated purpose was dose-finding and assessment of APD403 for preventing nausea and vomiting caused by chemotherapy.

The listed arms were Control, PLACEBO, APD403 10MG, ADP421 20MG, and APD421 40MG. The primary outcome record gives counts of 37 of 66 for Control, 13 of 66 for PLACEBO, 27 of 63 for APD403 10MG, 21 of 68 for ADP421 20MG, and 20 of 65 for APD421 40MG. These are participant counts with a delayed-phase complete response, not continuous measurements.

Arm descriptions state that the Control regimen was OND + DEX + FOS followed by oral DEX. The placebo regimen was OND + APD403 followed by oral PLACEBO; the low-, mid-, and high-dose regimens were OND + APD403 followed by oral APD403 at the corresponding dose. The registry separately lists ondansetron, placebo, dexamethasone, fosaprepitant, APD403 IV, and APD403 oral as interventions.

The primary endpoint description says analyses were conducted separately in strata of chemotherapy regimen and gender, and in strata of country. The registry record does not report the randomization ratio, detailed allocation procedure, masking assignments, dose amounts for the dose groups beyond the arm labels, or the original sample-size justification. The reported enrollment and arm counts describe the trial record but do not supply those missing design details.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: ITT

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 With Delayed Phase Complete Response(CR), measured over 24-120 hours.

The primary endpoint is the number of participants with delayed-phase complete response (CR) in the period from 24 to 120 hours after initiation of chemotherapy. CR is defined as absence of emetic episodes and no use of rescue medication during that interval. The outcome therefore combines two criteria: no recorded emetic episode and no rescue treatment. A participant must satisfy both to meet the stated definition.

This binary endpoint is useful for expressing whether participants met a clinically interpretable response definition during the delayed period. It also makes the arm results readily readable as counts of participants with the outcome, alongside the number assessed in each group. It does not show how often nausea occurred when vomiting was absent, the severity or duration of nausea, or the timing of any symptoms within the interval; those details are not part of the endpoint definition reported in the registry record.

The delayed-phase timeframe distinguishes the primary outcome from the secondary overall-phase CR outcome, which covers 0 to 120 hours after chemotherapy initiation. The endpoints thus share a response concept but refer to different observation windows. Their counts should not be treated as measurements of exactly the same period.

The registry identifies the primary population as ITT. It does not give further detail about how missing outcome observations were handled or how the stratified analyses were combined. Those omissions matter when interpreting a binary endpoint because the reported counts alone do not describe the handling of participants without an observed response assessment.

7. Results Posted in the Registry

• PLACEBO: 19.7% (13/66) versus 56.1% (37/66) on control; risk difference -36.4 percentage points (95% CI -51.7 to -21.0), risk ratio 0.35 (0.21–0.60); unadjusted two-proportion z-test p = <0.001.
• APD403 10MG: 42.9% (27/63) versus 56.1% (37/66) on control; risk difference -13.2 percentage points (95% CI -30.3 to 3.9), risk ratio 0.76 (0.54–1.09); unadjusted two-proportion z-test p = 0.134.
• ADP421 20MG: 30.9% (21/68) versus 56.1% (37/66) on control; risk difference -25.2 percentage points (95% CI -41.4 to -8.9), risk ratio 0.55 (0.36–0.83); unadjusted two-proportion z-test p = 0.003.
• APD421 40MG: 30.8% (20/65) versus 56.1% (37/66) on control; risk difference -25.3 percentage points (95% CI -41.7 to -8.9), risk ratio 0.55 (0.36–0.84); unadjusted two-proportion z-test p = 0.004.

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 CR in the Overall Phase.

• 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:
  • Placebo: 16.7% (11/66) versus 50.0% (33/66) on control; risk difference -33.3 percentage points (95% CI -48.4 to -18.3), risk ratio 0.33 (0.18–0.60); unadjusted two-proportion z-test p = <0.001.
  • APD403 10MG: 33.3% (21/63) versus 50.0% (33/66) on control; risk difference -16.7 percentage points (95% CI -33.4 to 0.1), risk ratio 0.67 (0.44–1.02); unadjusted two-proportion z-test p = 0.055.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between APD403 10MG and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is overall-phase CR from 0 to 120 hours after chemotherapy initiation. It uses the same general response definition—absence of emetic episodes and no rescue medication use—but covers a longer period than the delayed-phase primary outcome. Counts are posted for Control, PLACEBO, and the dose groups. The registry reports secondary comparisons for PLACEBO versus APD403 10MG and PLACEBO versus the group labelled APD403 20MG; it does not list a corresponding reported analysis for the highest-dose label in that secondary analysis record.

Across the secondary counts, Control has more participants meeting the overall-phase response definition than PLACEBO, and each posted APD403 dose-group count is between those two arms’ counts or otherwise below Control’s count. These are descriptive count patterns only. They should not be read as a separate confirmation of the primary endpoint, because the observation window differs and the sponsor’s reported tests and the simple recalculations do not necessarily use the same contrast or method.

The registry gives corrected chi-squared analyses for two secondary comparisons. Their reported p-values are 0.024 for PLACEBO versus APD403 10MG and 0.165 for PLACEBO versus the group labelled APD403 20MG. These sponsor-reported secondary results are distinct from the unadjusted recalculated comparisons. They also do not provide effect estimates or intervals in the record.

Secondary findings generally carry less inferential weight than a prespecified primary outcome because they may involve additional questions and comparisons. The registry record does not state whether these secondary analyses were adjusted for multiplicity, how they were prioritized, or whether all intended secondary outcomes are posted. A secondary p-value should therefore be interpreted in the context of the primary endpoint, the differing timeframe, the comparison method, and the unreported multiplicity plan, rather than as independent proof of a treatment effect.

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

• Number of Participants With CR in the Overall Phase.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the CR definition during the delayed phase or did not. For a binary endpoint, an arm’s observed response count is the number meeting the definition, while its group size is the number represented in that outcome record. The posted counts make the numerator and denominator explicit. The unadjusted recalculations compare those arm-level summaries without incorporating the stratification described in the endpoint record.

What does a risk difference describe?

A risk difference expresses the contrast between the observed proportions with the event—in this case, complete response—in two groups. Here the recalculated estimate is presented with the first listed arm as the comparison direction against Control. A negative estimate means the response proportion is lower in that named group than in Control; it does not mean that the outcome itself is negative. For example, the listed PLACEBO-versus-Control estimate is -0.364. The point estimate summarizes the observed contrast, but it does not show how much uncertainty surrounds it; the interval gives additional information.

Why are there multiple measures of association?

The recalculations also include risk ratios and odds ratios. A risk ratio compares the response proportions between groups, whereas an odds ratio compares the odds of response. These measures use different scales and should not be read as though their numerical values mean the same thing. For PLACEBO versus Control, the posted risk-ratio estimate is 0.351 and the posted odds-ratio estimate is 0.192. Their intervals are also reported. The registry’s sponsor analyses use logistic regression, a method that models the odds of a binary outcome. The record does not provide the fitted model coefficients, covariate details, or confidence intervals for those sponsor analyses.

What do the p-values tell the reader?

A p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an observed difference. The p-values from the simple recalculations are unadjusted. The sponsor’s reported p-values come from analyses described as logistic regression for the primary outcome. As the comparison groups differ, those p-values answer different comparison questions and should not be ranked as though they came from one identical analysis.

The record describes separate stratified analyses by chemotherapy regimen and gender, and by country. Stratification can account for the defined groups in the analysis, but the registry does not give enough detail to reconstruct the procedure, determine whether estimates were pooled, or assess how the reported p-values relate to each stratum. The unadjusted calculations do not reproduce that stated analysis plan.

Why can over-dispersion matter?

Over-dispersion is a general concern when variability in observed outcomes exceeds what a model assumes. For binary outcomes, the appropriate model and its assumptions depend on the data structure and analysis. The registry does not report over-dispersion diagnostics or a method addressing it, so there is no basis to state that it occurred in this trial. This is a general statistical consideration, not a reported finding.

Finally, statistical significance should be read alongside effect estimates, interval widths, design details, and multiplicity. The posted record includes several arms and outcomes, while the adjustment plan for multiple comparisons is not reported. A small p-value in an unadjusted comparison does not by itself establish that the comparison was prespecified, multiplicity-controlled, or clinically important.

11. Confidence Intervals and Precision

The intervals around the recalculated risk differences communicate uncertainty in the estimated arm contrasts. For PLACEBO versus Control, the estimate is -0.364 and the interval extends from -0.517 to -0.210. For APD403 10MG versus Control, the interval is -0.303 to 0.039. For the two arms labelled ADP421 20MG and APD421 40MG in the primary outcome record, the intervals are -0.414 to -0.089 and -0.417 to -0.089, respectively. These estimates are all based on the posted arm counts.

An interval gives a range of values compatible with the data under the method used to construct it. It is not a guarantee that the true value lies within its endpoints, and its width reflects statistical precision as well as sample size and the observed data. The APD403 10MG interval includes zero, while the other three recalculated intervals do not. The registry record does not state the confidence level or the interval-construction method for these recalculations, so those details should not be inferred from the endpoints alone.

The posted intervals apply to the unadjusted recalculations, not to the sponsor’s logistic-regression comparisons. The sponsor’s primary analysis entries report p-values but no estimate or interval. Thus, the posted inferential information is not identical across analyses, and a reader cannot use the recalculated interval as though it were an interval from the sponsor’s model.

Intervals also do not address sources of uncertainty that are not represented by the calculation, such as unreported missing-data handling, the multiplicity approach, or ambiguity in arm naming. Nor do they establish whether a difference matters clinically. They describe precision for a statistical contrast, subject to the analysis and data represented.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations give participants per arm for the binary outcomes; they are not total-event counts. Their assumptions are a two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm associated with an 80% chance of detecting the specified effect under those planning assumptions, if the assumptions hold. The 90% power column gives the corresponding per-arm figure for 90% power. These are planning quantities, not descriptions of what happened in the trial. The illustration is calculated from the observed effect and is not observed power.

Rows that plan for 100% of the observed effect use the full observed contrast as the target for the illustration. Rows for 75% and 50% of the observed effect consider progressively smaller target contrasts. Smaller effects generally require more participants to detect, which is why the planning figures rise as the assumed effect fraction decreases. This relationship is a general feature of statistical planning, while the particular figures depend on the posted estimates and the stated assumptions.

The calculations are not a reconstruction of the trial’s design or evidence that the trial was adequately or inadequately sized. They do not account for design features not included in the stated planning assumptions, such as the registry’s stratified analyses or any multiplicity adjustment. They are best read as conditional illustrations for two-arm comparisons, not as proof about the power of the completed study.

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 = 0.561; treatment proportion p₁ = 0.197; average p̄ = 0.379.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6860 = 1.3446.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6360 = 0.5353.
4. n = (1.3446 + 0.5353)² / (-0.3636)² = 26.7, rounded up to 27 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 <- 0.560606060606061                          # control proportion
p1 <- 0.196969696969697                          # 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(1857232)
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 = 27 (80% power), 36 (90% power)
 75% of observed effect: n per arm = 51 (80% power), 67 (90% power)
 50% of observed effect: n per arm = 118 (80% power), 157 (90% power)
power.prop.test: 26.7 
Simulated power at n = 27 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 the sponsor’s primary analyses as logistic regression comparisons between PLACEBO and dose groups. The reported p-values are 0.004 for PLACEBO versus APD403 10MG, 0.099 for PLACEBO versus the group labelled APD421 20MG in the primary outcome counts, and 0.104 for PLACEBO versus the group labelled APD421 40MG. The sponsor entries do not include effect estimates or confidence intervals.

The recalculated primary comparisons instead compare each listed arm with Control and use unadjusted arm-level summaries. For example, the recalculated APD403 10MG contrast is against Control, not PLACEBO. A p-value from that calculation therefore does not answer the same question as the sponsor’s PLACEBO comparison. The same distinction applies to the other dose groups. The recalculated values should not be presented as corrections to or substitutes for the sponsor’s model.

The record flags a discrepancy between the posted summaries and the reported analyses. In that situation, the sponsor’s own analysis takes precedence for describing its intended inferential result. The available record does not explain the discrepancy or provide enough model detail to reproduce the sponsor’s analysis. Consequently, the unadjusted recalculations are useful as transparent descriptions of the posted counts, while the sponsor’s results remain the appropriate account of the sponsor-reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint description states that analysis was conducted separately in strata of chemotherapy regimen and gender, and in strata of country. The registry does not specify the statistical model used for each stratum, whether strata-specific estimates were combined, or how those analyses relate to the reported logistic-regression comparisons. That detail is not reported in the registry record.

Several arms are represented, and the record includes a primary outcome plus a secondary overall-phase outcome. Multiple comparisons can increase the chance of at least one apparently unusual result when each is assessed separately. The registry record does not report a multiplicity adjustment, a hierarchy of hypotheses, or which comparisons were designated confirmatory. The sponsor’s primary analysis entries identify superiority comparisons, but that alone does not establish a family-wise error plan. The recalculated p-values are explicitly unadjusted.

The primary population is identified as ITT, but the record does not describe the precise analysis-set definition or how participants with missing endpoint information were handled. It does not report the number of missing outcome observations, imputation methods, sensitivity analyses, or exclusions from the endpoint analysis. The arm counts give outcome denominators, but those counts by themselves do not explain whether all randomized participants contributed to the analysis.

These omissions limit assessment of how robust the reported results are to missing data and how the multiplicity of outcomes and comparisons was handled. They do not show that missing data or multiplicity problems occurred; rather, they leave those features unresolved. No interim-analysis plan, stopping rule, or other monitoring procedure is reported in the registry record. The original statistical analysis plan and sample-size justification are also not reported, so the published record does not support reconstruction of the full prespecified analysis strategy.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5.0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: nausea (6.1%), neutropenic sepsis (3.1%), pyrexia (3.0%), febrile neutropenia (3.0%), renal failure (1.6%).

The adverse-event record lists participants at risk and participants affected by serious adverse events for each arm. It reports 8 of 66 for Control, 12 of 66 for Placebo, 2 of 63 for APD403 10MG, 3 of 68 for APD403 20MG, and 4 of 65 for the group labelled ADP403 40MG. These are participant counts, not event rates calculated. The registry also lists deaths as 2 in Control and 0 in each other listed group.

The record’s listed serious-event terms include Nausea at 6.1%, Neutropenic sepsis at 3.1%, Pyrexia at 3.0%, Febrile Neutropenia at 3.0%, Renal Failure at 1.6%, and Chest Pain at 1.5%. The registry excerpt does not specify the timeframe for these figures, the event-level counts behind each term, or whether the listed term percentages use the full study population as their denominator. They should not be assumed to describe arm-specific risks.

These figures are descriptive safety information. They do not by themselves establish comparative safety, especially without details on event ascertainment, exposure duration, severity grading, or adjustment for differences in group size. The arm label for the highest dose also differs across parts of the record, so the posted naming should be retained when reading the counts.

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

The posted results describe how many participants met the delayed-phase complete-response definition in each arm and report several statistical comparisons. The simple unadjusted comparisons indicate fewer observed complete responses in PLACEBO and in the dose groups than in Control, with varying estimates and precision. The registry’s own analyses address PLACEBO-versus-dose comparisons and report logistic-regression p-values. Since those analyses use different comparisons from the recalculations, the results should be kept distinct.

A response count is not a complete account of symptoms, and CR does not capture every dimension of nausea and vomiting. It records whether both stated conditions—no emetic episodes and no rescue medication use—were met in a specified period. It does not give symptom intensity, duration, or individual experiences. The overall-phase secondary endpoint has a broader timeframe and is not interchangeable with the delayed-phase primary endpoint.

The numerical results do not alone establish a causal interpretation. The registry identifies randomization and masking, but important details about allocation, missing observations, multiplicity, model specification, and the original sample-size plan are not reported. The sponsor’s analyses are the appropriate source for the sponsor-reported inference, while the recalculated unadjusted results provide a separate description based on the posted summaries. Neither set of numbers should be extended beyond its comparison and stated analysis.

These results also do not establish whether any observed contrast is clinically important. Statistical intervals and p-values characterize features of the data under analytical assumptions; they do not substitute for clinical interpretation or broader evidence. The record supports a careful account of the trial’s posted outcomes and their uncertainty, not a treatment recommendation or a conclusion about effects outside the participants and settings represented in this study.

18. Why This Trial Matters Statistically

This trial illustrates why the comparison being tested matters as much as the numerical result. The unadjusted recalculations use Control as the reference group, while the sponsor’s primary analyses compare PLACEBO with the dose groups. Those contrasts answer different questions. A p-value cannot be interpreted in isolation from the groups, endpoint, and model that generated it.

It also shows the value of separating observed counts from model-based inference. Counts such as 37 of 66 in Control and 13 of 66 in PLACEBO are direct descriptions of the posted outcome record. Risk differences and their intervals summarize an unadjusted comparison, while logistic regression represents the sponsor’s stated method. A transparent account keeps those layers visible rather than treating them as interchangeable.

The record includes a primary endpoint, a secondary endpoint with a different observation window, several dose groups, stratified-analysis statements, and safety counts. This creates several interpretive questions: how comparisons were prioritized, how multiplicity was handled, and how missing endpoint information was treated. The registry does not answer all of them. Their absence is important because a p-value alone cannot reveal the full analysis strategy.

Finally, the naming differences across the posted arms show that consistency in trial records is not merely editorial. Clear arm labels are necessary for aligning outcomes, analyses, and safety summaries. The statistical lesson is to describe exactly which comparison and record label are being discussed, and to distinguish what the data show from what the available analysis details leave unresolved.

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.

Several trial-specific limitations constrain interpretation. The registry record identifies the primary population as ITT but does not describe missing outcome handling, the number of missing assessments, or sensitivity analyses. The posted arm denominators therefore do not, on their own, show how all randomized participants were represented in the primary analysis.

The primary outcome description mentions analyses stratified by chemotherapy regimen and gender, and by country, but the record does not provide the model specifications, stratum-level results, or method for combining them. The sponsor’s logistic-regression entries provide p-values without effect estimates or intervals. The recalculated estimates are unadjusted and use Control as the reference, whereas the sponsor comparisons use PLACEBO. The discrepancy between the posted summary calculations and sponsor analyses is not explained.

Multiplicity handling is not reported, despite multiple arms and a secondary endpoint. The record also does not report the original sample-size assumptions, interim analyses, stopping rules, or a full statistical analysis plan. The planning illustrations are based on observed effects and stated assumptions; they cannot fill in the trial’s original design rationale.

There are naming inconsistencies: the primary outcome lists ADP421 20MG and APD421 40MG, while other parts of the record use APD403 labels. The available record does not establish whether these differences are typographical or reflect another distinction. The serious-event figures also lack event timeframe and denominator details for the listed terms. These limitations do not invalidate the posted counts, but they restrict how confidently the results can be aligned, reproduced, and generalized.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose-finding Study of APD403 to Prevent Nausea and Vomiting After Chemotherapy — NCT01857232.
• Registry record last updated 2020-11-25; status last verified 2020-11.
• Results first posted 2019-03-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed randomized, double-blind, dose-finding Phase II parallel-group study with enrollment of 342. It evaluated APD403 in participants receiving cisplatin- or AC-based chemotherapy. The primary outcome was delayed-phase CR from 24 to 120 hours after chemotherapy began, defined by no emetic episodes and no rescue medication use.

Primary response counts are posted for Control, PLACEBO, and three dose groups. The sponsor’s reported primary analyses use logistic regression for PLACEBO-versus-dose comparisons; separate unadjusted recalculations compare each listed group with Control. The registry record flags a discrepancy, so the sponsor’s own analysis takes precedence when describing sponsor-reported inference. The secondary outcome concerns overall-phase CR from 0 to 120 hours.

The record also includes serious adverse-event counts and deaths. Important details—including the original sample-size justification, missing-data procedures, multiplicity plan, and fuller model specifications—are not reported in the registry record. Arm naming varies across record entries, which adds uncertainty when aligning results across outcomes.