Steroid-sparing Therapy (Olanzapine) Versus Dexamethasone-based Therapy for Chemotherapy-induced Nausea and Vomiting: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Steroid-sparing Therapy (Olanzapine) Versus Dexamethasone-based Therapy for Chemotherapy-induced Nausea and Vomiting (NCT05590923), a randomized phase 4 study. The primary outcome is Number of Patients With Complete Response (CR) Over 120 Hours Following Chemotherapy.

2. Clinical Question

The trial addressed whether a steroid-sparing antiemetic regimen using olanzapine could provide complete response over 120 hours following chemotherapy, compared with a dexamethasone-based regimen. Complete response was defined as no emesis and no use of rescue antiemetic medication. The comparison was framed as a non-inferiority question in the official title, but the registry record does not report a non-inferiority margin or a statistical analysis testing that claim. Its posted results are counts, not a completed inferential analysis from the trial investigators.

The trial used a crossover arrangement: participants were assigned to a sequence in which they received one treatment after cycle 1 and crossed over to the other treatment after cycle 2. This means treatment observations were linked to chemotherapy cycles within the assigned sequence, rather than simply representing two unrelated groups of participants. The registry record does not report a formal analysis accounting for that design.

3. Trial Design

This was a randomized, phase 4, open-label trial described in its official title as single center and non-inferiority. The allocation was randomized, masking was none, and the model was crossover. The study compared olanzapine with dexamethasone in people receiving high- or moderate-emetogenic chemotherapy. Enrollment was 23. The record lists the study as terminated and states that it was terminated without statistical analysis.

Participants were assigned to one of two sequences. In the OLA-then-DEX sequence, olanzapine was used after chemotherapy cycle 1 and dexamethasone after cycle 2. In the DEX-then-OLA sequence, dexamethasone was used after cycle 1 and olanzapine after cycle 2. The listed olanzapine regimen was 10 mg orally each night on days 1-4 after high-emetogenic chemotherapy or days 1-3 after moderate-emetogenic chemotherapy. The dexamethasone regimen was 8 mg orally daily on days 2-4 after high-emetogenic chemotherapy or days 2-3 after moderate-emetogenic chemotherapy.

The cycle length depended on the physician’s decision and standard-of-care protocols for each cancer type. The record does not describe whether, or how, the analysis accounted for treatment sequence, period, within-participant correlation, or possible differences between chemotherapy cycles. Although the posted outcome counts list 23 observations for each treatment, the relationship between those outcome denominators and the crossover sequences is not described in enough detail to reconstruct participant-level data.

The trial’s non-inferiority framing is important, but the registry record does not report the planned non-inferiority margin, the original sample-size justification, or a completed non-inferiority analysis. It also does not report a statistical plan for the crossover design. The posted figures therefore describe the recorded outcome counts and simple contrasts, not a documented trial analysis establishing non-inferiority.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Study was terminated without statistical analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients With Complete Response (CR) Over 120 Hours Following Chemotherapy, measured over 120 hours following chemotherapy.

The primary endpoint was the number of participants with complete response over 120 hours following chemotherapy. Complete response (CR) meant absence of emesis and no use of a rescue antiemetic medication. The endpoint covered the acute phase, within 24 hours after chemotherapy; the delayed phase, from 24 hours through 120 hours; and the overall period through 120 hours. The record notes that chemotherapy cycle length varied according to physician decision and standard-of-care protocols for each cancer type.

A count endpoint expresses how many participants met a prespecified outcome definition during a specified time window. Here, the definition combines an observed symptom outcome, emesis, with use of rescue medication. That combination makes the endpoint a measure of complete control under the trial’s stated criteria, rather than a measure of nausea intensity alone. The registry does not provide a separate nausea severity scale as part of this primary endpoint.

For a treatment comparison, the counts can be expressed as event proportions and contrasted. Such a contrast describes the observed difference in the proportion meeting the response definition. It does not, by itself, establish that one treatment caused a difference, especially when the design is crossover and the registry record reports no formal analysis. The endpoint’s use for a non-inferiority question would also require a prespecified margin and an analysis suited to that question; those details are not reported in the registry record.

7. Results Posted in the Registry

• OLA (Olanzapine): 60.9% (14/23) versus 39.1% (9/23) on control; risk difference 21.7 percentage points (95% CI -6.5 to 49.9), risk ratio 1.56 (0.85–2.85); unadjusted two-proportion z-test p = 0.140.

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 Patients With Complete Control (CC) Over 120 Hours Following Chemotherapy

• 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:
  • OLA (Olanzapine): 56.5% (13/23) versus 39.1% (9/23) on control; risk difference 17.4 percentage points (95% CI -11.0 to 45.8), risk ratio 1.44 (0.77–2.69); unadjusted two-proportion z-test p = 0.238.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OLA (Olanzapine) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients With Total Control (TC) Over 120 Hours Following Chemotherapy

• 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:
  • OLA (Olanzapine): 43.5% (10/23) versus 34.8% (8/23) on control; risk difference 8.7 percentage points (95% CI -19.4 to 36.8), risk ratio 1.25 (0.60–2.59); unadjusted two-proportion z-test p = 0.546.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OLA (Olanzapine) and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary outcomes follow the same broad descriptive direction as the primary endpoint: the olanzapine counts and estimated proportions are higher than the dexamethasone counts and proportions. Across complete control and total control, the size of the estimated risk difference is smaller than for complete response, and the uncertainty intervals are broad and include zero. The corresponding unadjusted p-values do not provide evidence of a precise separation between treatments. These patterns add descriptive context but do not resolve the uncertainty in the primary comparison.

Complete control and total control are related to the primary complete-response outcome, but they are distinct recorded outcomes. They should not be treated as interchangeable measures or as independent replications of the primary result. The primary endpoint’s definition includes absence of emesis and no rescue antiemetic use; the registry lists the secondary outcomes by name but does not give their operational definitions in the posted outcome descriptions. No additional assumptions about their definitions are warranted.

The registry lists 12 outcome measures, while two secondary outcomes are posted with results. In general, when multiple outcomes or comparisons are examined, the chance of finding an apparently noteworthy result can increase unless the analysis plan addresses multiplicity. The record does not report a hierarchy among outcomes, an adjustment procedure, or a formal analysis for the secondary outcomes. Their unadjusted results therefore carry less weight as confirmatory evidence and are best read as descriptive alongside the primary outcome.

Because the study was terminated without statistical analysis, the secondary contrasts also do not come with reported analyses accounting for the crossover structure. They cannot be used to make a formal claim that one treatment is superior, equivalent, or non-inferior. Taken together, the secondary outcomes are directionally consistent with the primary count pattern, but their uncertainty and the absence of a reported analysis limit the strength of any overall interpretation.

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

• Number of Patients With Complete Control (CC) Over 120 Hours Following Chemotherapy
• Number of Patients With Total Control (TC) Over 120 Hours Following Chemotherapy

9. Statistical Interpretation

10. Statistical Methods Explained

The main posted comparison is a risk difference: the response proportion for olanzapine minus the response proportion for dexamethasone. It is a measure on the absolute proportion scale. A value of zero would correspond to equal observed response proportions; a positive value indicates a larger observed proportion for olanzapine, and a negative value indicates a larger proportion for dexamethasone. The estimate is 0.217. This is an unadjusted contrast calculated from the posted summary counts, rather than an estimate from a reported trial model.

What does a confidence interval describe?

In general, a confidence interval expresses uncertainty around an estimate under the statistical method used. The primary endpoint’s 95% confidence interval runs from -0.065 to 0.499. Because it includes zero, the counts are compatible with no risk difference under this calculation; they are also compatible with effects in either direction. The interval’s breadth is relevant: it indicates substantial imprecision, so the point estimate alone should not be treated as a settled estimate of the comparative effect.

What does the p-value add?

The posted unadjusted p-value is 0.14. In general, a p-value is calculated under a null hypothesis and model, and describes how unusual data at least as extreme as those observed would be if that null model were true. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result is due to chance. This p-value is unadjusted, and the registry reports no formal statistical analysis. It should not be treated as a test of non-inferiority or equivalence.

Why does the crossover design matter?

In a crossover trial, a participant receives treatments in a sequence, so outcomes on different treatments can be linked within the same person. General statistical methods for crossover data can account for that pairing and may consider treatment sequence and period. Such methods can use within-participant information, but they require adequate design and analysis details. The registry record does not report a model, a period or sequence analysis, or any other formal analysis. The risk difference and p-value posted for the primary endpoint are therefore best understood as unadjusted summary-statistic calculations, not as a documented crossover-model result.

For general context, treating paired observations as if they came from independent groups can misrepresent uncertainty when within-person responses are correlated. The degree and direction of that correlation cannot be recovered from the aggregate counts. Nor can the posted counts show whether treatment effects differed by sequence or chemotherapy cycle. Those questions would require participant-level outcomes and analysis details that are not reported in the registry record.

What does the non-inferiority framing require?

In general, a non-inferiority trial asks whether the uncertainty around the treatment contrast rules out an unacceptable loss relative to a comparator. That decision depends on a prespecified non-inferiority margin, a direction for the contrast, and an analysis plan suited to the design. A conventional test for a difference does not answer that question by itself. The registry record labels the study non-inferiority in its title, but the margin and formal analysis are not reported. The posted risk difference and unadjusted p-value cannot therefore be interpreted as a non-inferiority conclusion.

What does the absence of an analysis mean?

The primary outcome description states that the study was terminated without statistical analysis. The record lists zero analyses. This means the posted results do not include a reported investigator analysis or model-based estimate that can be evaluated for adjustment, assumptions, or handling of the crossover. A simple recalculation from summary statistics can help describe the recorded counts, but it cannot recover unreported trial methods or substitute for the sponsor’s analysis. No discrepancy is flagged in the record, but the absence of a reported analysis remains a limitation.

The endpoint is binary at the participant level: a participant either met the complete-response definition or did not during the specified window. Counts and proportions are useful descriptions of binary outcomes, but their precision depends on the amount of information and the underlying response frequency. Here, the recorded counts are small and the confidence interval is wide. General statistical interpretation should therefore emphasize uncertainty alongside the point estimate, particularly given the crossover design and the absence of a reported formal analysis.

Finally, the record identifies 12 outcome measures, while two secondary outcomes are posted with results. A collection of outcomes can raise multiplicity concerns if many comparisons are examined and selectively emphasized. General methods for addressing multiplicity include prespecifying a hierarchy or adjusting inference, but the registry record does not report whether any such approach was planned or used. The secondary comparisons should be interpreted descriptively rather than as stand-alone confirmatory evidence.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.217, and its 95% confidence interval extends from -0.065 to 0.499. The lower endpoint is below zero and the upper endpoint is above zero. Thus, the interval does not isolate a single direction of effect: it includes a possible advantage for dexamethasone, no difference, and a possible advantage for olanzapine under the calculation used. The interval also reaches values substantially different from the point estimate, indicating that the estimate is not precise.

In general, a confidence interval is a way to show the uncertainty associated with an estimate, conditional on the statistical method and assumptions. It is not a guarantee that the true value lies in the particular interval, and it does not account for sources of uncertainty that the method omits. In this case, the posted calculation does not come from a reported crossover analysis. The interval should not be assumed to account for within-participant dependence, treatment sequence, or period effects.

The listed count for each treatment was 23, and the registry reports that the study was terminated without statistical analysis. These features make the uncertainty important to the interpretation. A numerical difference between the counts does not provide a precise estimate of a treatment contrast, and the p-value does not narrow the interval or resolve the design questions. The registry record does not report a non-inferiority margin against which to evaluate the interval.

Precision is distinct from whether a result crosses a conventional statistical threshold. The interval’s inclusion of zero and the unadjusted p-value of 0.14 do not establish equality, nor do they establish non-inferiority. They describe uncertainty under the simple comparison. Any stronger claim would require a prespecified inferential target and a suitable analysis of the crossover data, neither of which is reported in the registry record.

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 event counts. They are illustrations based on the observed effect, rather than a reconstruction of the trial’s original design. The stated 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 set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target chance of detecting that effect, and therefore generally calls for more participants. For the primary outcome, planning for 100% of the observed effect gives 82 participants per arm for 80% power and 110 participants per arm for 90% power. Planning for 75% of the observed effect gives 147 participants per arm for 80% power and 195 participants per arm for 90% power. Planning for 50% of the observed effect gives 328 participants per arm for 80% power and 438 participants per arm for 90% power.

The pattern reflects a general planning principle: smaller effects are harder to distinguish from random variation, so detecting them with the same target power requires more participants. These figures are sensitive to the assumptions used, including the observed effect that anchors the illustration. They are not evidence that the trial had a particular probability of finding a result, and they are not observed power. The registry record does not report the trial’s own planned sample size calculation or whether a calculation was used for its non-inferiority design.

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 = 0.391; treatment proportion p₁ = 0.609; average p̄ = 0.500.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3859.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6902 = 0.5809.
4. n = (1.3859 + 0.5809)² / (0.2174)² = 81.9, rounded up to 82 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 <- 0.391304347826087                          # control proportion
p1 <- 0.608695652173913                          # 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(5590923)
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 = 82 (80% power), 110 (90% power)
 75% of observed effect: n per arm = 147 (80% power), 195 (90% power)
 50% of observed effect: n per arm = 328 (80% power), 438 (90% power)
power.prop.test: 81.9 
Simulated power at n = 82 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, time point, subgroup, or comparison. In general, examining many results can increase the chance that at least one appears noteworthy by chance. Prespecifying a primary outcome and a hierarchy for secondary outcomes, or using an appropriate adjustment, can help control how the results are interpreted. The registry identifies one primary endpoint and lists 12 outcome measures, with two secondary outcomes posted. It does not report a multiplicity strategy, a testing hierarchy, or an adjustment procedure.

The registry record lists zero analyses and states that the study was terminated without statistical analysis. It does not report whether any interim analyses were planned or performed. It also does not report analysis populations, such as whether the primary analysis was intended to include all randomized participants, participants who completed both treatment periods, or another defined group. The handling of missing outcome data, incomplete cycles, withdrawals, or deviations from the assigned sequence is not reported in the registry record.

For a crossover trial, analysis-population definitions can matter because treatment comparisons may depend on which participants contribute observations for both periods. The record does not say whether the posted denominators include all randomized participants, only those with recorded outcomes, or another set. It also does not report whether sequence, period, or within-participant correlation was included in an analysis. The outcome counts cannot establish how any missing or incomplete data were handled.

The non-inferiority designation makes the missing analysis details especially consequential. The registry record does not report a non-inferiority margin, the trial’s original sample-size justification, a prespecified analysis population for non-inferiority, or the statistical plan. Without those elements, the posted counts and simple contrasts do not answer the stated non-inferiority question. The record’s termination without statistical analysis should be kept separate from any inference about the treatments themselves: it describes the status and analysis available, not a conclusion about comparative efficacy.

These are reporting gaps in the registry record. They do not establish that a particular method was absent from the original protocol or that a particular analysis was conducted elsewhere. The record does not report those details, so they cannot be inferred from the outcome summaries.

15. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The safety figures list 23 participants at risk in each treatment group. There were zero serious adverse events in the dexamethasone group and zero in the olanzapine group. For other adverse events, the record lists one participant affected in the dexamethasone group and zero in the olanzapine group. Deaths were zero in both groups. No serious adverse event terms are listed.

These are counts over the reported safety groups. They do not describe the severity, timing, duration, or causal attribution of the other adverse event, and those details are not reported in the registry record. The record also does not provide a formal safety comparison or a statistical analysis of adverse events. A count of zero reported serious events is not proof that no such events could occur; it describes what was recorded for the listed groups in this terminated study.

The crossover structure and the limited number of participants also matter when interpreting safety summaries. The record does not clarify how adverse events occurring in different treatment periods were attributed or whether the listed groups represent participants, treatment exposures, or another reporting unit. The figures should therefore be read as registry counts, not as a complete estimate of comparative safety.

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

The registry record shows that the primary complete-response count was 14 for olanzapine and 9 for dexamethasone, with 23 listed for each treatment. The simple risk-difference estimate was 0.217, with a 95% confidence interval from -0.065 to 0.499 and an unadjusted p-value of 0.14. This is a descriptive comparison of posted counts with substantial uncertainty. It does not establish that either treatment is better, worse, equivalent, or non-inferior.

The official title describes a non-inferiority trial, but the record does not report the non-inferiority margin or a formal analysis. A failure to obtain a small p-value in a conventional difference test is not proof of equivalence, and it does not demonstrate that a non-inferiority criterion was met. Those conclusions require a prespecified margin and an analysis designed for that purpose, particularly in a crossover trial.

The registry states that the study was terminated without statistical analysis. The comparisons do not therefore represent a reported investigator analysis accounting for the crossover structure. The aggregate counts cannot reveal the relationship between each participant’s outcomes across treatment periods or how treatment sequence and cycle effects might influence the result. They also do not provide enough information to determine how missing outcomes were handled.

The posted adverse-event figures report zero serious adverse events in either group, one other adverse event in the dexamethasone group, zero in the olanzapine group, and zero deaths. These counts describe the safety data recorded in the registry, but they do not support a broad conclusion about comparative safety. Details about event characteristics and attribution are not reported.

Overall, the result is best understood as a small, incomplete registry record with posted counts and unadjusted contrasts. It can inform a description of what was recorded, but it cannot answer the intended non-inferiority question or establish a treatment effect. It is not a basis for medical advice.

17. Why This Trial Matters Statistically

This trial illustrates why the design and the analysis must be interpreted together. A crossover trial exposes participants to both treatments in a sequence, making the relation between outcomes within the same participant potentially important. A comparison based only on aggregate treatment counts cannot show that relation. Without a reported analysis that accounts for the crossover, it is not possible to tell whether the posted uncertainty reflects the design’s paired structure or whether sequence and period were considered.

The trial also demonstrates the difference between a trial’s stated objective and the evidence available to assess it. The official title identifies a non-inferiority objective, but the registry record does not report the margin, original sample-size assumptions, or a completed statistical analysis. A non-inferiority label does not itself establish that the design or analysis met the requirements for such a conclusion. The posted counts and conventional unadjusted comparison are not a substitute for those details.

Precision is another central issue. The primary estimate is accompanied by a broad confidence interval that includes both negative and positive risk differences. That uncertainty is more informative than focusing on the point estimate alone. Planning illustrations based on the observed effect also show how strongly required sample size depends on the effect selected for detection, though they do not describe the trial’s original planning.

Finally, registry outcome counts and safety counts can be useful even when a formal analysis is unavailable, provided their limits are explicit. Here, the record states that the study was terminated without statistical analysis and provides no reported analyses. Clear separation between descriptive evidence, unadjusted calculations, and a sponsor’s formal trial analysis prevents the numerical summaries from being read as stronger evidence than they are.

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 main limitation is that the registry record states the study was terminated without statistical analysis and lists zero analyses. The posted outcome counts therefore lack a reported formal analysis of the randomized crossover design. There is no reported estimate from a model that accounts for outcomes being linked within participants, treatment sequence, or chemotherapy-cycle period.

The listed enrollment is 23, and the outcome counts list 23 for each treatment. Because the study crossed participants between treatments, the record does not clarify how the denominators relate to participants, treatment periods, or available outcomes. It does not report whether all participants completed both cycles, whether any data were missing, or how incomplete or unavailable outcomes were handled.

The non-inferiority objective is not accompanied by a reported margin, trial-specific sample-size justification, or formal non-inferiority analysis. The record also does not report analysis populations, multiplicity methods, interim analyses, or a prespecified statistical plan. The original sample-size assumptions are not reported; the displayed planning illustrations use the observed effect and different assumptions.

The trial was open label, with no masking. The record does not report whether outcome assessment was blinded. The cycle length varied according to physician decision and standard-of-care protocols for each cancer type, and the record does not describe an analysis addressing potential variation across chemotherapy regimens or cycles. Safety-event descriptions and attribution are also limited. These gaps restrict interpretation of both the effectiveness counts and the safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Steroid-sparing Therapy (Olanzapine) Versus Dexamethasone-based Therapy for Chemotherapy-induced Nausea and Vomiting — NCT05590923.
• Registry record last updated 2026-09-02; status last verified 2025-10.
• Results first posted 2026-09-02.
• 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

NCT05590923 was a phase 4 randomized, open-label, crossover trial comparing olanzapine with dexamethasone for chemotherapy-induced nausea and vomiting. Its official title describes a single-center non-inferiority trial. The registry lists enrollment of 23 and status as terminated. Participants were assigned to receive the treatments in opposite sequences across chemotherapy cycles.

The primary endpoint was the number of participants with complete response over 120 hours following chemotherapy, defined as absence of emesis and no rescue antiemetic use. The posted counts were 9 for dexamethasone and 14 for olanzapine, with 23 listed for each treatment. The unadjusted risk difference was 0.217, with a 95% confidence interval from -0.065 to 0.499 and an unadjusted p-value of 0.14.

The registry states that the study was terminated without statistical analysis and lists no reported analyses. The record does not report the non-inferiority margin, original sample-size justification, or methods for handling the crossover, missing data, or multiplicity. The outcome and safety counts should be interpreted descriptively, with substantial uncertainty.