An Efficacy and Safety Study of Oral Netupitant and Palonosetron for the Prevention of Nausea and Vomiting: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Efficacy and Safety Study of Oral Netupitant and Palonosetron for the Prevention of Nausea and Vomiting (NCT01339260), a randomized phase 3 study. The primary outcome is Percentage of Patients With Complete Response (CR) Defined as no Emesis, no Rescue Medication, at Cycle 1.

2. Clinical Question

The registry describes the study objective as assessing whether the combination of netupitant and palonosetron is more effective than palonosetron alone for preventing nausea and vomiting associated with moderately emetogenic chemotherapy over repeated cycles. The primary endpoint addresses a defined post-chemotherapy window in the first cycle, rather than the entire experience across all cycles. It is a binary outcome: each participant either meets the complete-response definition for that window or does not.

The comparison is between treatment regimens, not between netupitant and palonosetron as isolated ingredients. Dexamethasone was included in both arms, but its recorded dose differed: 12 mg with the combination and 20 mg with palonosetron alone. The registry record therefore describes the efficacy contrast between these assigned regimens. It does not isolate the contribution of any one component.

3. Trial Design

The registry identifies NCT01339260 as a completed Phase III randomized, quadruple-masked, parallel-group, active-controlled study. It was a multicenter study, according to its official title. The enrollment recorded in the registry is 1455. The study began in 2011-04, and primary completion was recorded as 2012-11. Helsinn Healthcare SA is listed as the sponsor.

Participants were assigned to one of two oral regimens. One arm received netupitant/palonosetron (300 mg/0.50 mg) and dexamethasone (12 mg); the other received palonosetron 0.50 mg and dexamethasone (20 mg). Both regimens were scheduled for Day 1 before each chemotherapy cycle. The study title describes double-blind and double-dummy methods, while the registry’s masking field labels masking as quadruple. The exact roles concealed by masking are not reported in the registry record.

The primary reported outcome is complete response in cycle 1 during 25-120 hours. The registry lists 724 in the combination arm and 725 in the palonosetron arm for this endpoint, with the analysis population labelled FAS. Safety records describe cycle 1 groups at risk of 725 in each arm, as well as separate multicycle-extension groups. The extension records are distinct safety summaries; the registry record does not give enough information to infer how participants entered or completed that extension.

The record lists two additional complete-response outcomes, for 0-24 hours and 0-120 hours in cycle 1. This provides information about different time windows, but does not establish that the same analysis procedures were used for every endpoint. Further details on randomization procedures, allocation concealment, masking roles, and the original sample-size justification 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: 1455 patients randomized (ITT population), 1450 received study drug i.e. netupitant/palonosetron combination or palonosetron, both with dexamethasone, in cycle 1 (safety population-cycle 1), 1449 received chemotherapy and study drug (FAS), 1286 received study drug in multi-cycle extension (safety population-multi-cycle extension)

Cycle 1

Multi-cycle Extension

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

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: Safety population ie patients receiving either netupitant/palonosetron combination or palonosetron, both plus dexamethasone

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Patients With Complete Response (CR) Defined as no Emesis, no Rescue Medication, at Cycle 1, measured over 25-120 hours.

The primary endpoint is the percentage of patients with complete response in cycle 1, defined as no emesis and no rescue medication, over 25-120 hours. The registry identifies the analysis population as FAS and gives a 95% confidence interval for each arm’s response percentage. A complete-response endpoint combines two clinically relevant components into a single binary classification: occurrence of emesis and use of rescue medication both prevent a participant from meeting the definition.

In the combination arm, the reported response was 76.9% (95% CI 73.7 to 79.9); in the palonosetron plus dexamethasone arm, it was 69.5% (95% CI 66.1 to 72.8). These are percentages of participants meeting the endpoint definition, not measures of the number or severity of individual episodes. The endpoint also does not separately describe nausea that occurs without emesis or rescue medication.

A prespecified time window makes the outcome interpretable in relation to chemotherapy timing. The 25-120-hour window addresses the period after the first 24 hours and through the stated end of the cycle 1 assessment window. The registry also reports outcomes for other windows, but they represent different endpoint definitions and should not be treated as interchangeable with the primary endpoint.

Complete response is useful for a comparative trial because it turns a composite of two observable criteria into an outcome that can be counted across treatment groups. It gives a direct responder proportion while necessarily compressing the underlying experiences into a yes-or-no classification. The record does not report additional detail about how emesis or rescue-medication use was collected or adjudicated.

7. Results Posted in the Registry

• Palonosetron Plus Dexamethasone: 69.5% (504/725) versus 76.9% (557/724) on control; risk difference -7.4 percentage points (95% CI -12.0 to -2.9), risk ratio 0.90 (0.85–0.96); 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 Patients With Complete Response (CR) Defined as no Emesis, no Rescue Medication at Cycle 1

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Palonosetron Plus Dexamethasone: 85.0% (616/725) versus 88.4% (640/724) on control; risk difference -3.4 percentage points (95% CI -6.9 to 0.1), risk ratio 0.96 (0.92–1.00); unadjusted two-proportion z-test p = 0.055.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Palonosetron Plus Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Patients With Complete Response (CR) Defined as no Emesis, no Rescue Medication, at Cycle 1

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Palonosetron Plus Dexamethasone: 66.6% (483/725) versus 74.3% (538/724) on control; risk difference -7.7 percentage points (95% CI -12.4 to -3.0), risk ratio 0.90 (0.84–0.96); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Palonosetron Plus Dexamethasone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry reports two secondary complete-response outcomes for cycle 1: one covers 0-24 hours, and the other covers 0-120 hours. Across these windows, the overall direction is consistent with the primary comparison: the combination arm has a higher reported response proportion. The early-window comparison is less conclusive than the primary and full-window comparisons, while the 0-120-hour outcome gives a pattern more closely aligned with the primary result.

These outcomes help describe how the observed response pattern varies across assessment windows. They do not represent independent replications of the primary endpoint: they come from the same trial and concern related response definitions in the same cycle. Their results can add context, but should not be treated as three unrelated confirmations. A difference in statistical evidence across windows can reflect the outcome rates, the precision of the estimates, and the specific time interval being assessed.

The registry reports sponsor analyses for the secondary outcomes and also supports simple unadjusted recalculations. The secondary findings should carry less inferential weight than a primary result when no multiplicity procedure or prespecified testing hierarchy is reported. Testing several outcomes increases the opportunity for at least one apparently strong result to arise by chance. The registry record does not report whether these secondary tests were adjusted, how they were ordered, or whether any testing hierarchy governed interpretation.

Accordingly, the secondary pattern is best read as supportive descriptive context rather than as a separate definitive claim. The primary result remains the central statistical finding because it is the designated primary endpoint. The additional windows broaden the description of cycle 1 response but do not resolve the unreported details of multiplicity control or the missing-data approach.

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

• Percentage of Patients With Complete Response (CR) Defined as no Emesis, no Rescue Medication at Cycle 1
• Percentage of Patients With Complete Response (CR) Defined as no Emesis, no Rescue Medication, at Cycle 1

9. Statistical Interpretation

10. Statistical Methods Explained

In general, a randomized parallel-group trial compares outcomes between groups assigned to different interventions. Randomization is intended to make the groups comparable at baseline on average, including with respect to factors that are measured and those that are not. The registry identifies this study as randomized and parallel-group, but does not report the sequence-generation or allocation-concealment details. A reader should therefore distinguish the design label from procedural details that are not reported.

What does a binary response measure?

In general, a binary endpoint assigns each participant to one of two outcome categories, such as meeting or not meeting a response definition. The primary endpoint is defined as no emesis and no rescue medication in the stated assessment window. The arm percentages estimate the proportion meeting that definition in the analysis population. Binary endpoints are straightforward to summarize, but they do not show the range, timing, frequency, or severity of experiences within either category.

The same binary outcome can be compared using multiple effect measures. A risk difference subtracts one group’s response probability from the other’s, so it expresses an absolute difference and its sign depends on the subtraction order. A risk ratio divides one probability by the other. An odds ratio compares odds, where odds are the probability of response divided by the probability of not responding. These measures answer related but nonidentical questions; an odds ratio is not itself a difference in percentages. The registry reports an odds ratio from the Cochran-Mantel-Haenszel analysis, while the simple recalculation reports a risk difference.

What does the Cochran-Mantel-Haenszel method contribute?

In general, the Cochran-Mantel-Haenszel method combines information across strata to estimate an association while accounting for the stratification. It is often used for categorical outcomes. The registry reports this method and an odds ratio of 1.48 for the primary comparison, with a 95% confidence interval from 1.16 to 1.87 and p = 0.001. The particular stratification variables and further model details are not reported in the registry record. It is therefore possible to describe the named method and reported estimate, but not to reconstruct the sponsor’s full analysis.

The unadjusted re-calculation uses the posted group counts and sizes to make a direct comparison of response proportions. It does not reproduce the reported Cochran-Mantel-Haenszel procedure. The two estimates are close in their overall interpretation, but their calculation methods differ. The registry does not flag a discrepancy; the sponsor’s reported analysis remains the primary inferential result.

How should p-values be read?

In general, a p-value describes how incompatible the observed data, or more extreme data, are with a specified null model, assuming that model and the testing procedure are appropriate. It does not quantify the size or importance of an effect. A small p-value is not a measure of how likely the finding is to be true, and it does not establish that all relevant sources of bias or uncertainty have been addressed. For the primary analysis, the registry reports p = 0.001. The re-calculation also reports p = 0.001, using a different, unadjusted comparison.

Interpretation should also consider the confidence interval and the outcome scale. The odds ratio interval ranges from 1.16 to 1.87, while the direct risk-difference interval ranges from -0.120 to -0.029 for the stated arm order. The former describes uncertainty on an odds scale; the latter describes uncertainty on a probability-difference scale. Neither interval captures every uncertainty relevant to generalizing beyond this study, such as differences between trial participants and other populations.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation is greater than a statistical model expects. For binary outcomes, it can arise when participants’ outcomes are more variable or clustered than the model assumes. If a method ignores important over-dispersion, standard errors can be too small and confidence intervals too narrow. If it accounts for variation that is not present, estimates can instead be less precise. No over-dispersion assessment or related model detail is reported in the registry record, so it is not possible to say whether this issue arose in the sponsor’s analysis.

What does masking add?

In general, masking can reduce the risk that expectations influence care, outcome assessment, or reporting. The study title describes double-blind and double-dummy methods, and the registry masking field says quadruple. The record does not state which participants, investigators, assessors, or other roles were masked, or how masking success was evaluated. The design labels are informative, but they do not substitute for those details.

The registry also labels the primary population FAS, but does not define membership or describe the handling of participants with missing outcome information. Those details matter because the analysis population and missing-data rules can affect a binary response estimate. The registry names the main reported method and gives the principal result, while leaving several parts of a complete statistical analysis plan not reported in the registry record.

11. Confidence Intervals and Precision

A confidence interval expresses the range of estimates that are reasonably compatible with the data under the method used and its assumptions. In general, a 95% confidence interval is produced by a procedure that would cover the true parameter in 95% of repeated studies conducted under the same conditions. It is not a statement that there is a 95% probability that this particular fixed interval contains the true value.

For the primary endpoint, the combination arm’s response estimate is 76.9%, with a 95% confidence interval from 73.7 to 79.9. The palonosetron plus dexamethasone arm’s estimate is 69.5%, with a 95% confidence interval from 66.1 to 72.8. These intervals communicate uncertainty around each arm’s response proportion. They are not a substitute for an interval around the between-arm contrast.

The reported odds ratio is 1.48, with a 95% confidence interval from 1.16 to 1.87. The interval lies above the null value for an odds ratio, which is 1. The recalculated risk difference, expressed as the palonosetron arm minus the combination arm, is -0.074, with a 95% confidence interval from -0.120 to -0.029. That interval lies below the null value for a difference, which is zero. These results convey the direction and precision of the primary comparison on two different scales.

In general, narrower intervals indicate greater statistical precision, while wider intervals indicate more uncertainty about the effect’s magnitude. Precision is not the same as freedom from bias: an interval can be narrow even when the study has limitations in its conduct or applicability. The reported interval also reflects the analysis method and its assumptions; it does not account automatically for unreported analytical choices, missing-data concerns, or multiplicity.

The arm-specific intervals overlap to some extent, but overlap between separate arm intervals is not the appropriate test of the treatment contrast. The interval for the comparison itself is more directly relevant to the uncertainty about the difference or ratio. Readers should use the sponsor’s reported contrast and its interval for the primary inferential result, and treat the unadjusted re-calculation as a transparent check based on the posted summaries.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not a report of the trial’s original design calculation. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

For 80% power, the planning figure is the number of participants per arm that would give the stated chance of detecting the chosen effect under those assumptions, if that effect were the true effect and the assumptions held. The 90% power column uses a higher target chance of detecting that effect and therefore requires more participants per arm. These are design-planning concepts, not statements about the probability that the observed study result is true.

For the primary endpoint, planning for 100% of the observed effect gives 559 participants per arm for 80% power and 747 participants per arm for 90% power. Planning for 75% of the observed effect gives 972 participants per arm for 80% power and 1,300 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,135 participants per arm for 80% power and 2,858 participants per arm for 90% power. The pattern illustrates the general principle that smaller effects are harder to distinguish from chance variation and therefore require more participants.

The curve is a way to view how the planning requirement changes as the assumed effect changes; it does not describe participants’ observed outcomes or the trial’s actual probability of success. These figures are not observed power. They are prospective-style calculations constructed from an observed effect for illustration, and the registry record does not report that they were used to design this trial.

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 = 0.769; treatment proportion p₁ = 0.695; average p̄ = 0.732.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6262 = 1.2273.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6240 = 0.5252.
4. n = (1.2273 + 0.5252)² / (-0.0742)² = 558.4, rounded up to 559 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 <- 0.769337016574586                          # control proportion
p1 <- 0.695172413793103                          # 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(1339260)
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 = 559 (80% power), 747 (90% power)
 75% of observed effect: n per arm = 972 (80% power), 1,300 (90% power)
 50% of observed effect: n per arm = 2,135 (80% power), 2,858 (90% power)
power.prop.test: 558.4 
Simulated power at n = 559 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is a Cochran-Mantel-Haenszel analysis of the odds ratio. It reports an odds ratio of 1.48, a 95% confidence interval from 1.16 to 1.87, and p = 0.001. The re-calculation is an unadjusted comparison of the posted summary counts and expresses the result as a risk difference, with an estimate of -0.074, a 95% confidence interval from -0.120 to -0.029, and p = 0.001. The negative difference uses the palonosetron arm relative to the combination arm.

These statistics use different scales and different procedures. An odds ratio compares odds, while a risk difference compares response probabilities; the numerical values should not be compared as if they measured the same quantity. The recalculation is a check on the direction and broad pattern of the posted data, not a recreation of the sponsor’s stratified analysis. The registry record flags no discrepancy between the analyses. The sponsor’s own analysis takes precedence for the trial’s reported inferential result.

The registry does not report enough detail to reproduce every aspect of that analysis, including the stratification variables. The recalculated p-value is unadjusted and should be read with that limitation in mind. Neither agreement in direction nor similar evidence against a null comparison removes uncertainty about the effect’s magnitude, the analysis population, or the study’s applicability.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses or endpoints are tested. In general, as the number of statistical tests increases, the chance of at least one false-positive result can increase if each test is judged separately at the same significance threshold. Common approaches include prespecifying a hierarchy, adjusting significance thresholds, or controlling an error rate across a family of tests. The registry record lists a primary endpoint and two secondary complete-response outcomes, but does not report a multiplicity adjustment, testing hierarchy, or family of hypotheses.

The primary result can be described using its reported estimate, confidence interval, and p-value. However, the record does not establish whether the primary test was considered within a larger family of endpoints or whether the reported inference was adjusted for other analyses. The sponsor reports Cochran-Mantel-Haenszel analyses for the primary and secondary outcomes. That information identifies a method, but does not describe the broader testing strategy. The secondary results therefore merit more cautious interpretation when their relationship to a prespecified multiplicity plan is not reported.

The record labels the primary analysis population FAS. The meaning of the label in this trial, the criteria for inclusion, and the handling of participants who did not complete the assessment are not reported in the registry record. The registry gives arm denominators for the primary outcome, but does not explain whether missing outcomes were excluded, imputed, or handled through another rule. Missing-data methods can affect estimated response proportions, particularly when missingness differs across groups or is related to outcome status.

Interim analyses, stopping rules, and the original sample-size justification are not reported in the registry record. The registry does contain planning illustrations based on the observed effect, but those are not evidence of the trial’s original design assumptions. Randomization, masking, the named primary analysis method, and the posted endpoint results are reported; details beyond these should not be inferred. These unreported features limit how fully an independent reader can reconstruct the confirmatory statistical plan.

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 (0.9%), neutropenia (0.9%), anaemia (0.3%), leukopenia (0.3%), stomatitis (0.3%).

The registry reports serious adverse event counts for the cycle 1 safety groups: 13 in the netupitant/palonosetron plus dexamethasone group and 12 in the palonosetron plus dexamethasone group, each with 725 at risk. It also reports other adverse event counts of 551 and 507, respectively, with 725 at risk in each cycle 1 group. These are counts, not estimates of the causal effect of either regimen, and the record does not provide a comparative statistical analysis for these safety summaries.

For the multicycle extension, the registry lists serious adverse events in 23 of 635 at risk in the combination group and 15 of 651 at risk in the palonosetron group. Other adverse events are listed as 533 of 635 and 527 of 651, respectively. The extension is reported separately from cycle 1; its groups and denominators should not be merged with the cycle 1 safety figures. The record does not explain the extension entry or follow-up process in enough detail to interpret differences in exposure.

Listed serious-event terms and percentages include febrile neutropenia (0.9%), neutropenia (0.9%), anaemia (0.3%), leukopenia (0.3%), stomatitis (0.3%), and urinary tract infection (0.3%). Death counts are not reported in the registry record. Counts alone do not establish comparative risk: exposure time, event definitions, severity detail, and statistical uncertainty are not fully described in these summaries.

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

The primary statistical result is that the recorded complete-response proportion in cycle 1 during 25-120 hours was higher in the netupitant/palonosetron plus dexamethasone arm than in the palonosetron plus dexamethasone arm. The sponsor’s reported odds ratio is 1.48, with a 95% confidence interval from 1.16 to 1.87 and p = 0.001. The simple unadjusted risk-difference recalculation is in the corresponding direction and has a confidence interval that does not include zero.

This is a result about the trial’s defined outcome and comparison. Complete response means no emesis and no rescue medication within the stated window. It does not measure every dimension of nausea and vomiting, does not convey the experience of each participant, and does not distinguish the separate contributions of the drugs in either regimen. Because the dexamethasone doses differ between arms, the trial compares the full regimens as recorded rather than isolating the effect of netupitant alone.

The finding does not establish that the same response pattern applies to every chemotherapy regimen, patient group, treatment setting, or cycle. The primary endpoint is specifically from cycle 1, while the registry provides separate outcomes for other cycle 1 time windows and safety summaries for a multicycle extension. Those additional data do not, by themselves, show that the primary effect persists across all cycles.

The result also does not constitute a complete safety assessment. The registry reports adverse-event counts and selected serious-event terms, but the posted summaries do not include a full analysis of comparative safety, exposure, or uncertainty. Nor does a statistically significant result by itself establish the clinical importance of an effect. The size and precision of the estimate, the endpoint definition, the treatment context, and the limitations of the registry record all matter to interpretation.

In general, trial results support conclusions about the groups and procedures studied, subject to the quality of the design and analysis. Randomization and masking are reported, but details about missing outcomes, multiplicity, allocation procedures, and the original statistical plan are not reported in the registry record. These gaps limit independent assessment of some aspects of the evidence and caution against extending the result beyond the comparison and time window actually recorded.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters in a two-arm study with a binary response. The sponsor reports an odds ratio, while a direct re-calculation gives a risk difference. Both are legitimate ways to express a comparison, but they have different interpretations and numerical scales. Reporting the underlying response proportions alongside the comparative estimate helps readers understand the outcome context rather than relying on a single relative measure.

It also shows the value of reading a confidence interval with a point estimate. The primary result is not just a p-value: its interval communicates uncertainty about the comparative effect, while the arm-specific intervals communicate uncertainty in each response estimate. Statistical evidence against a null comparison does not remove uncertainty about the exact magnitude or the applicability of the result outside the trial.

The study’s related secondary windows demonstrate why multiple outcomes require careful interpretation. Results from several assessment windows may describe a coherent pattern, but they are not independent replications, and the record does not report how multiplicity was handled. A statistically sound reading gives priority to the designated primary endpoint and treats secondary outcomes in light of the missing testing-plan details.

Finally, the registry record makes a distinction between the sponsor’s own analysis and an unadjusted calculation based on posted group summaries important. Recalculation can serve as a transparent consistency check, but it cannot substitute for unavailable analysis details. This is a practical example of how statistical interpretation combines effect scale, precision, analysis method, endpoint definition, and reporting completeness rather than reducing a trial to whether a p-value crosses a threshold.

19. Limitations

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

Several trial-specific details needed for a full appraisal are not reported in the registry record. These include the original sample-size justification, randomization sequence and allocation-concealment procedures, the roles masked under the masking design, and the detailed analysis plan. The registry names the Cochran-Mantel-Haenszel method for the reported analyses, but does not identify the strata or provide enough detail to reproduce that procedure independently.

The primary population is labelled FAS without a trial-specific definition. Handling of missing outcome data, protocol deviations, and participants who did not complete the assessment is not reported in the registry record. This makes it difficult to determine exactly how the analysis population was formed or whether missingness could have affected the responder proportions. Interim analyses and stopping rules are also not reported.

The record lists two secondary complete-response outcomes, but does not report multiplicity control or a hierarchy for their interpretation. This matters because multiple related tests can make nominal p-values less persuasive when no adjustment strategy is known. The secondary outcomes provide context for cycle 1, but are not independent confirmations of the primary comparison.

The comparison evaluates full regimens with different dexamethasone doses, so the contrast cannot isolate the contribution of a single drug. The primary endpoint is limited to a specific cycle 1 window, and the safety summaries include separate cycle 1 and multicycle-extension groups without a detailed account of extension participation or exposure. The registry’s serious and other adverse-event counts are descriptive and do not include comparative uncertainty estimates in the posted summaries. These reporting limitations do not negate the reported primary finding, but they constrain how completely the study’s analysis, safety profile, and broader applicability can be evaluated.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: An Efficacy and Safety Study of Oral Netupitant and Palonosetron for the Prevention of Nausea and Vomiting — NCT01339260.
• Registry record last updated 2014-11-26; status last verified 2014-11.
• Results first posted 2014-11-26.
• 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

NCT01339260 is a completed randomized Phase III, quadruple-masked, parallel-group, active-controlled study sponsored by Helsinn Healthcare SA. The registry records enrollment of 1455, a start date of 2011-04, and primary completion in 2012-11. The study compared oral netupitant/palonosetron plus dexamethasone with oral palonosetron plus dexamethasone in cancer patients receiving moderately emetogenic chemotherapy.

The primary endpoint was cycle 1 complete response, defined as no emesis and no rescue medication during 25-120 hours. The reported response was 76.9% in the combination arm and 69.5% in the palonosetron arm. The sponsor’s Cochran-Mantel-Haenszel analysis reported an odds ratio of 1.48 (95% CI 1.16 to 1.87; p = 0.001). The record also includes two secondary response windows and safety summaries. Details on multiplicity, missing-data handling, and the original sample-size justification are not reported in the registry record.