Ondansetron Plus Dexamethasone With or Without Metoclopramide as Antiemetic Prophylaxis After Receiving Cisplatin: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ondansetron Plus Dexamethasone With or Without Metoclopramide as Antiemetic Prophylaxis After Receiving Cisplatin (NCT01093690), a randomized na study. The primary outcome is Number of Patients Who Had Complete Response.

2. Clinical Question

The registry describes a randomized, placebo-controlled trial with triple masking and a parallel-group design. The clinical question is therefore a comparison of two add-on strategies against a common antiemetic background, rather than a comparison of the shared background regimen with no prophylaxis. The posted primary outcome is a count of participants meeting the complete-response definition in each group.

The registry’s stated objective was to assess the efficacy and tolerability of adding metoclopramide to the standard antiemetic regimen for prophylaxis of cisplatin-induced emesis. The record does not report a more detailed description of what constituted routine medical practice or how patients were selected. The disease stage, treatment setting details, and characteristics that might help judge how closely these participants resemble other clinical populations are not reported in the registry record.

3. Trial Design

The study is registered as randomized, triple-masked, and parallel-group. It compared a metoclopramide regimen with a placebo regimen, with both groups also receiving ondansetron and dexamethasone. The registered enrollment is 162. The registry status is completed; the study start is listed as 2009-04 and primary completion as 2010-06. The phase is recorded as NA, so a phase designation is not reported in the registry record.

The metoclopramide group received ondansetron 8 mg orally twice a day on days 2-5 and dexamethasone 8 mg orally twice a day on days 2-4, with metoclopramide 20 mg orally four times a day on days 2-5. The placebo group had the same ondansetron and dexamethasone schedules and received placebo 20 mg orally four times a day on days 2-5. The record identifies the placebo as a drug intervention and gives matching administration schedules.

The primary outcome was measured 5 days after receiving chemotherapy. The registry describes it as the number of patients who experienced no emesis and needed no rescue treatment during the 5-day period, using an intention-to-treat population. The posted arm counts are 50 of 83 in the metoclopramide group and 42 of 79 in the placebo group. These are the recorded outcome counts and group denominators; they do not describe the timing of individual events or the handling of any participants whose outcome status was unavailable.

The sponsor is Mahidol University. The registry does not report the randomization sequence generation, allocation concealment, exact masking procedures, or whether masking success was assessed. It also does not report the trial’s original sample-size justification or its planned statistical analysis details. Those omissions limit assessment of how the design and analysis were specified before outcomes were known.

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: All recruited patients were participate enrollment.

Overall Study

Analysis population for the primary outcome, as defined in the registry: intention to treat

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 Patients Who Had Complete Response, measured over 5 days after receiving chemotherapy.

The primary endpoint is the number of patients with a complete response during the 5 days after chemotherapy. The registry defines complete response as having no emesis and requiring no rescue treatment during that period. It is therefore a binary participant-level outcome: each participant either meets the stated definition or does not. The posted arm results count those who met the definition.

This endpoint combines two clinically relevant aspects of vomiting control: the occurrence of emesis and the need for additional rescue treatment. A patient must meet both parts of the definition to count as a complete responder. This can make the outcome easier to interpret as a single overall response measure, but it does not show which part of the definition drove a group result. Separate counts for emesis and rescue treatment are not reported in the registry record.

The registry specifies an intention-to-treat population, meaning the endpoint is presented for participants according to the assigned groups in the stated analysis population. The record does not explain how missing endpoint observations, treatment changes, or deviations from the assigned regimen were handled. The five-day timeframe also defines the scope of the primary result: it does not, on its own, describe symptoms or treatment use outside that period.

The registry lists toxicities and severity of nausea and vomiting as secondary outcomes. Details of their measurement, timing, and analysis are not reported in the registry record. The complete-response endpoint thus gives a focused summary of the registered primary question, while leaving symptom severity, individual endpoint components, and outcomes beyond the stated timeframe to other reported information, if any.

7. Results Posted in the Registry

• Metoclopramide: 60.2% (50/83) versus 53.2% (42/79) on control; risk difference 7.1 percentage points (95% CI -8.2 to 22.3), risk ratio 1.13 (0.86–1.49); unadjusted two-proportion z-test p = 0.363.

8. Statistical Interpretation

9. Statistical Methods Explained

For a binary endpoint, each participant is classified according to whether the defined event occurred. Here, the event is complete response: no emesis and no rescue treatment during the five-day period. The arm-level counts are the number meeting that definition, and the arm denominators are the numbers included in the posted outcome results. Reporting the count alongside the denominator lets readers see the observed response pattern without treating the raw counts alone as if the groups were the same size.

What does a risk difference describe?

A risk difference compares the event probability in one group with the event probability in the other by subtracting one probability from the other. A positive value in the direction used for this comparison means the observed complete-response probability is higher in the metoclopramide group. Unlike a relative measure, a risk difference expresses the contrast on the probability scale. It can be useful for understanding the absolute size and direction of a between-group contrast, but its interpretation still depends on the definition and timeframe of the outcome.

The posted recalculation gives a positive risk-difference point estimate. Its confidence interval crosses zero, the value corresponding to no difference on this scale. That means the point estimate alone is not a precise account of the plausible range of effects: values on either side of no difference remain compatible with the interval. The registry record does not report the confidence level for the interval, so a particular confidence percentage should not be assumed from the record.

What does the chi-squared test assess?

A chi-squared test evaluates whether the observed distribution of the binary outcome across groups is consistent with a hypothesis of no association between assigned group and outcome, subject to the assumptions of the test. The registry reports a chi-squared analysis with p = 0.41. The recalculated unadjusted test reports p = 0.363. A p-value measures how unusual data at least this discrepant from the null model would be if that model and the test assumptions held; it is not the probability that the null hypothesis is true, nor a measure of the probability that the result occurred by chance.

Interpretation of a p-value depends on the analysis plan, including the selected significance threshold and whether the comparison was designated in advance. The threshold used for the trial’s own primary analysis is not reported in the registry record. The sample-size planning assumptions list a two-sided significance level of 0.05 for the planning illustration; that assumption does not establish the trial’s original analysis threshold. A statistical test also does not tell readers whether an effect is important in practice. That requires considering the outcome, the estimate, its uncertainty, and context beyond the test alone.

Why are confidence intervals important?

A confidence interval communicates uncertainty around an estimate under the method used to construct it. It is not a range containing a known fixed percentage of future trial results, and it does not assign probabilities to individual values of the true effect. In general, wider intervals indicate less precision than narrower intervals. For the posted risk difference, the interval includes the no-difference value and reaches both negative and positive values. This shows that the data do not determine the direction of the underlying contrast precisely.

The record also lists relative measures, including a risk ratio and an odds ratio, with intervals. These measures compare groups on different scales. A risk ratio relates the event probabilities, whereas an odds ratio relates the event odds. Their null values differ from the null value for a risk difference: no relative difference corresponds to one for a ratio measure, while it corresponds to zero for a difference measure. The posted intervals for the ratio measures also span their respective null values. The risk difference is the most direct scale for describing an absolute probability contrast, while ratios can be useful for relative comparisons. None of these scales substitutes for the outcome definition or resolves uncertainty.

What can be inferred from the analysis population?

The primary endpoint is identified as intention to treat. In general, intention-to-treat analysis seeks to preserve the randomized comparison by analyzing participants according to their assigned groups, regardless of treatment received after assignment. The registry does not give operational details about this analysis, such as whether every randomized participant had an observed endpoint or what procedures were used for missing outcomes. Therefore, the label alone does not settle how all potential missing-data or protocol-deviation issues were handled.

The registry reports one sponsor analysis for the comparison and one posted secondary outcome category. It does not state how multiplicity across outcomes or analyses was handled. When many outcomes or comparisons are examined, the chance of at least one small p-value can increase; methods for controlling that issue depend on a prespecified plan. Whether such methods were used is not reported in the registry record. The posted result should therefore be understood in the context of the analysis information actually recorded, not as evidence that unreported analytic decisions were made in a particular way.

Why can unadjusted recalculations differ from a reported analysis?

A recalculation from arm-level counts is a simple unadjusted analysis of the posted summary data. A sponsor analysis may use a specified test or additional procedures that are not fully described in the registry. Differences can also arise from choices such as continuity corrections or the exact statistical implementation, but the registry does not identify such choices for this result. The recalculated p-value is therefore supplementary. The sponsor’s reported chi-squared result remains the trial’s own posted analysis, and the registry’s record is the source for what that analysis reported.

These methods address different parts of interpretation. Counts describe the observed outcomes, an effect estimate describes the direction and scale of the group contrast, a confidence interval conveys uncertainty, and a test gives a p-value under a null model. None alone answers every clinical question. The statistical result should be read as a comparison of the registered groups and endpoint, with the limitations in outcome detail, missing-data reporting, and analysis-plan information kept in view.

10. Confidence Intervals and Precision

The posted risk-difference estimate is positive, but its confidence interval extends across no difference, from the negative side to the positive side. This is an important distinction: the observed comparison points toward more complete responses in the metoclopramide group, while the interval indicates that the direction and size of the underlying group contrast remain uncertain. The interval is not narrow enough to exclude differences in either direction.

Confidence intervals describe sampling uncertainty under the method used to calculate them. They do not account automatically for every source of uncertainty, such as bias in measurement, differences between the trial participants and another population, or unreported analysis choices. The confidence level associated with the posted interval is not reported in the registry record. No specific confidence percentage should therefore be attached to it based on this record alone.

The posted relative measures also have intervals that include their no-association value. That is consistent with the risk-difference interval’s broad directional uncertainty, although each measure is on a different scale. The estimate and interval should be read together: the estimate summarizes the observed contrast, while the interval shows that the data are compatible with a range of effects.

The group outcome counts, 50 of 83 and 42 of 79, are the basis of the posted binary comparison. Even with randomization, estimates from a trial remain subject to sampling variation. The registry does not report a formal precision target or the trial’s original sample-size assumptions, so the available information does not show what degree of uncertainty the study was designed to resolve. The sample-size planning illustration is based on the observed effect and should not be confused with evidence that the estimate is precise.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants and not total events. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its reference and illustrates planning for 100%, 75%, and 50% of that observed effect. The original design assumptions and sample-size justification for the trial are not reported in the registry record.

For planning at 100% of the observed effect, the figures are 769 participants per arm for 80% power and 1,029 participants per arm for 90% power. For planning at 75% of the observed effect, the figures are 1,374 participants per arm for 80% power and 1,838 participants per arm for 90% power. For planning at 50% of the observed effect, the figures are 3,104 participants per arm for 80% power and 4,154 participants per arm for 90% power.

In general, the 80% power column represents the planned number per arm under which a study would have an 80% chance of detecting the specified effect if that effect were real and the assumptions held. The 90% column uses a higher chance of detection and therefore requires more participants in these illustrations. Smaller effects are harder to detect, so planning for a smaller fraction of the observed effect requires more participants per arm.

These are planning illustrations, not observed power. They are calculated from the observed effect and do not reconstruct the trial’s original planning process. The trial’s own sample-size assumptions, including its target effect and any allowance for loss of outcome information, are not reported in the registry record.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.532; treatment proportion p₁ = 0.602; average p̄ = 0.567.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7007 = 1.3734.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6989 = 0.5882.
4. n = (1.3734 + 0.5882)² / (0.0708)² = 768.4, rounded up to 769 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 <- 0.531645569620253                          # control proportion
p1 <- 0.602409638554217                          # 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(1093690)
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 = 769 (80% power), 1,029 (90% power)
 75% of observed effect: n per arm = 1,374 (80% power), 1,838 (90% power)
 50% of observed effect: n per arm = 3,104 (80% power), 4,154 (90% power)
power.prop.test: 768.4 
Simulated power at n = 769 per arm: 0.799 (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.

13. Analyses Reported by the Sponsor

The registry’s own analysis is a chi-squared comparison and reports p = 0.41. The posted recalculation from the arm-level outcome counts is an unadjusted comparison and gives p = 0.363. The registry does not provide enough detail to reconcile the difference between these numerical results, including all implementation choices used in the sponsor analysis. The record does not flag a discrepancy.

The recalculated result is useful as a transparent check based on the posted counts, but it is not a substitute for the sponsor’s analysis. The sponsor result is the analysis reported by the trial record; the recalculation is a simple, unadjusted re-analysis of summary data. Neither p-value should be interpreted as an effect size or as a measure of clinical importance.

The direction of the observed arm counts and the positive recalculated risk-difference estimate favor the metoclopramide group numerically. At the same time, the risk-difference confidence interval includes no difference and values in both directions. The sponsor’s p-value and the recalculated p-value do not remove that uncertainty. The statistical methods and analysis population beyond the registry’s stated chi-squared method and intention-to-treat endpoint description are not reported in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The primary outcome is identified as an intention-to-treat comparison of complete response over the 5-day period after chemotherapy. The registry reports one analysis for the primary comparison and lists toxicities and severity of nausea and vomiting as secondary outcomes. It does not describe a hierarchy among outcomes, a family of confirmatory hypotheses, or a procedure for adjusting for multiple comparisons. Whether multiplicity was addressed in the trial’s analysis plan is not reported in the registry record.

Multiplicity matters because the more outcomes or statistical comparisons that are examined, the greater the chance that some result may appear unusual under a null model. This is a general statistical consideration, not a claim that a particular multiplicity problem occurred in this trial. Without the full prespecified analysis plan, it is not possible to determine which analyses were confirmatory, whether any were exploratory, or how any multiplicity was handled.

The registry labels the primary population as intention to treat, but does not give the operational details of the analysis. It does not state whether all randomized participants were included in the endpoint calculation, whether outcome data were missing, or how missing data were handled. The posted denominators are 83 for metoclopramide and 79 for placebo; the record does not explain their relationship to the randomized allocation process or describe exclusions, if any.

The record also does not explain how treatment discontinuations, deviations from the assigned regimen, or rescue treatment outside the endpoint definition were handled analytically. The endpoint definition does make rescue treatment part of the complete-response criterion, but further event-level detail is not reported. These gaps prevent a full assessment of the analysis population and the robustness of the primary comparison to missing outcome information.

Consequently, the available record supports describing the stated intention-to-treat endpoint and the posted group results, but not reconstructing all analysis decisions. The statistical analysis plan, missing-data rules, and multiplicity approach are not reported in the registry record.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry records serious adverse events for 0 of 83 participants at risk in the metoclopramide group and 0 of 79 participants at risk in the placebo group. These are the serious adverse event figures posted for the two groups. The absence of recorded events in these data should not be read as proof that no serious events could occur; the counts describe what the registry reports for this trial.

Other adverse events are recorded for 67 of 83 participants in the metoclopramide group and 62 of 79 participants in the placebo group. The registry does not provide the event terms, severity breakdown, or a detailed description of the reporting period for these other events. As a result, the counts alone cannot show which events occurred, how serious they were, or whether they differed in clinically meaningful ways.

Deaths are not reported in the registry record. The record lists no serious adverse event terms, but the absence of listed terms does not provide a detailed event-level safety account. These figures should be interpreted as the posted safety counts, not as a complete assessment of tolerability or comparative safety.

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

The primary endpoint asks whether participants had no emesis and needed no rescue treatment during the five days after chemotherapy. The observed counts were 50 of 83 in the metoclopramide group and 42 of 79 in the placebo group. The point estimate for the risk difference is positive, meaning the observed complete-response result was numerically higher with metoclopramide added to the shared ondansetron and dexamethasone regimen.

The interval around that estimate crosses no difference and extends to both sides. The registry’s chi-squared analysis reports p = 0.41, while the unadjusted recalculation reports p = 0.363. These results indicate uncertainty in the comparison; they do not establish that the regimens are equivalent, nor do they demonstrate that one regimen is superior. A failure to distinguish the groups statistically is not proof that their effects are identical.

The result applies to the registered comparison, outcome definition, and timeframe. Both groups received ondansetron and dexamethasone according to the listed schedules. The comparison therefore concerns adding metoclopramide rather than placebo, not the effect of the common antiemetic medicines themselves. The registry record does not establish that the result applies to different doses, different schedules, other chemotherapy regimens, or populations not described in the record.

The result also does not identify whether any difference in complete response was due to emesis, rescue treatment, or both. The primary outcome combines those components, and separate component results are not reported in the registry record. Secondary outcomes include toxicities and severity of nausea and vomiting, but the record does not provide detailed results for those outcomes in the information recorded.

The safest interpretation is descriptive: the posted counts and point estimate favor metoclopramide numerically, but the confidence interval and reported tests leave substantial uncertainty about the direction and size of the true contrast. The record does not support a definitive claim about benefit, lack of benefit, or comparative tolerability.

17. Why This Trial Matters Statistically

This trial illustrates why an observed difference and a statistical conclusion are not the same thing. The group counts favor metoclopramide numerically, and the risk-difference estimate is positive. Yet its interval includes no difference and extends in both directions. Looking only at the direction of the point estimate would leave out the uncertainty that matters when interpreting a randomized comparison.

It also shows why the outcome definition matters. Complete response requires both no emesis and no rescue treatment over the stated period. A single count gives a concise summary, but it cannot reveal which component contributed to the result. Clear endpoint definitions help readers understand what a statistical comparison does and does not measure.

The comparison is controlled by a shared regimen: ondansetron and dexamethasone are listed in both groups, with metoclopramide or placebo added. That design focuses the question on the added treatment within the registered regimen. It is important not to interpret the result as a test of the shared medicines or as an answer about all antiemetic approaches.

Finally, statistical reporting is strongest when the analysis plan, confidence level, missing-data procedures, and multiplicity approach are explicit. Several of those details are not reported in the registry record. The primary result can still be described, but the missing methodological information limits independent assessment of the analysis and the intended precision. This is a useful example of reading an effect estimate, uncertainty interval, test result, and reporting completeness together rather than relying on a single statistic.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record gives limited information about eligibility, baseline participant characteristics, cancer details, cisplatin schedules, and the clinical setting beyond routine medical practice. Without those details, readers cannot assess how representative the enrolled participants were or how directly the result applies to other groups receiving cisplatin.

The record describes randomization and triple masking but does not explain sequence generation, allocation concealment, or the practical masking procedures. It also does not report whether masking was assessed. These omissions limit evaluation of potential sources of bias, even though the design labels indicate that randomization and masking were intended.

For the primary endpoint, the definition and timeframe are stated, but the registry does not report the confidence level for the posted interval, the trial’s own significance threshold, or the full analysis plan. The handling of missing endpoint information, treatment deviations, and exclusions is not described. The intention-to-treat label is informative but does not fill in those operational details.

The registry does not report the original sample-size justification or the assumptions behind the trial’s own target enrollment. The planning illustration based on the observed effect is not a substitute for the original design rationale. The approach to multiple outcomes or analyses is also not reported, making it difficult to distinguish prespecified confirmatory analyses from other analyses.

Safety reporting is limited to group-level counts. The serious adverse event counts are recorded as 0 in each group, while other adverse event counts are given without event terms or severity detail. Death counts are not reported in the registry record. These limitations mean the posted safety information cannot provide a detailed comparison of specific harms or their severity.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Ondansetron Plus Dexamethasone With or Without Metoclopramide as Antiemetic Prophylaxis After Receiving Cisplatin — NCT01093690.
• Registry record last updated 2010-12-02; status last verified 2010-11.
• Results first posted 2010-12-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01093690 is a completed, randomized, triple-masked, parallel-group trial sponsored by Mahidol University. It compared metoclopramide with placebo as an addition to ondansetron and dexamethasone for antiemetic prophylaxis after high-dose cisplatin. The registered enrollment is 162, and the phase is recorded as NA.

The primary outcome was the number of participants with complete response, defined as no emesis and no rescue treatment during the 5 days after chemotherapy, in an intention-to-treat population. The posted counts were 50 of 83 for metoclopramide and 42 of 79 for placebo. The registry’s chi-squared analysis reports p = 0.41; the unadjusted recalculation reports p = 0.363. The risk-difference interval includes no difference.

The registry lists toxicities and severity of nausea and vomiting as secondary outcomes. Serious adverse event counts are 0 in both groups; other adverse event counts are 67 and 62, respectively. Further event details and several analysis-plan elements are not reported in the registry record.