An Umbrella Study Evaluating the Efficacy and Safety of Multiple Treatment Combinations in Patients With Gastric or Gastroesophageal Junction Carcinoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Umbrella Study Evaluating the Efficacy and Safety of Multiple Treatment Combinations in Patients With Gastric or Gastroesophageal Junction Carcinoma (NCT05251948), a randomized phase 1, phase 2 study. The primary outcome is Objective Response Rate (ORR).

2. Clinical Question

The comparison is therefore a question about the observed frequency of tumor response in these two treatment combinations, not a direct comparison of every possible treatment option for gastric or gastroesophageal junction carcinoma. The umbrella design allowed treatment arms and participant populations to change over time, so the posted arms should be understood within the study’s Stage 1 framework. The registry record does not report additional details that would support broader conclusions about other arms or populations.

3. Trial Design

This is a Phase Ib/II, open-label, multicenter, randomized umbrella study of treatment combinations in participants with gastric or gastroesophageal junction carcinoma. The registry lists an enrollment of 40 and a status of terminated. The start date is 2022-03-01, and the primary completion date is 2025-09-04. The reason for termination is not reported in the registry record.

The umbrella design was intended to permit new treatment arms to open as treatments became available, existing arms to close for minimal clinical activity or unacceptable toxicity, and the participant population to be modified. In the described Stage 1, eligible participants were randomly assigned to one of the available treatment arms. Participants experiencing loss of clinical benefit or unacceptable toxicity could be eligible for a different combination in Stage 2 when one was available and introduced by a protocol amendment. The record describes flexibility in the study structure, but does not report the history of every possible arm change.

The posted Stage 1 results cover Atezo + CAPOX and Atezo + CAPOX + Tira. The registry reports 18 participants for the former and 22 for the latter in the primary outcome results. Randomization can support a comparative interpretation, but the record does not report the allocation sequence, stratification factors, or other details needed to assess how randomization was implemented. No masking was used, so the study was open-label.

Participants in both described arms were treated until unacceptable toxicity or loss of clinical benefit as determined by the investigator. The primary outcome was assessed by the investigator. The registry record does not report whether an independent review of responses was performed, nor does it describe a protocol-specific sample-size justification or the original statistical design assumptions. Those omissions limit assessment of how the study was planned and how the posted analyses relate to its initial design.

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: Participants in Stage 1 were randomized to receive either atezolizumab (atezo) in combination with capecitabine and oxaliplatin (CAPOX) (control arm), or atezolizumab in combination with CAPOX and tiragolumab (tira) (experimental arm). As pre-specified in the Protocol, the sponsor decided not to open the Stage 2 part of the study for enrollment.

Stage 1

Reasons for not completing this period:

Long-term Survival Follow-up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy-evaluable population included all participants who received at least one dose of each drug for their assigned treatment regimen.

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: All Randomized Population included randomized participants, grouped according to the treatment assigned.

6. Primary Endpoint

The registry lists the primary outcome as Objective Response Rate (ORR), measured over Up to 42.1 months.

The primary endpoint, objective response rate (ORR), is the percentage of participants with a complete response or partial response during Stage 1. A response had to be recorded on two consecutive occasions at least four weeks apart and was determined by the investigator according to RECIST v1.1. A complete response required disappearance of all target and non-target lesions, with pathological lymph nodes reduced to less than 10 millimeters in short axis. A partial response required at least a 30% decrease in the sum of diameters of target lesions from baseline, without meeting the complete-response definition.

ORR is a binary outcome at the participant level: each participant is classified as having or not having a qualifying response. It is often used to describe whether measurable tumor shrinkage occurred during a specified treatment period. It does not by itself describe how long a response lasts, whether disease later progresses, overall survival, symptoms, or quality of life. Those questions require other outcomes, some of which are listed as secondary outcomes in this study.

Participants with missing or no response assessments were classified as non-responders. That rule is important when interpreting the percentages, because the endpoint does not exclude such participants from the response classification. The efficacy-evaluable population was defined as participants who received at least one dose of each drug in their assigned regimen. The registry gives the primary outcome timeframe as up to 42.1 months.

7. Results Posted in the Registry

• Atezo + CAPOX + Tira: 40.9% (9/22) versus 55.6% (10/18) on control; risk difference -14.6 percentage points (95% CI -45.5 to 16.2), risk ratio 0.74 (0.38–1.41); unadjusted two-proportion z-test p = 0.356.

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.

Disease Control Rate (DCR)

• 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:
  • Atezo + CAPOX + Tira: 72.7% (16/22) versus 77.8% (14/18) on control; risk difference -5.1 percentage points (95% CI -31.8 to 21.7), risk ratio 0.94 (0.66–1.33); unadjusted two-proportion z-test p = 0.714.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atezo + CAPOX + Tira and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover several different questions, including disease control, progression-free survival, overall survival, survival at specified timepoints, duration of response, and adverse events. The available binary summary for disease control shows rates of 77.8% for Atezo + CAPOX and 72.7% for Atezo + CAPOX + Tira. Its unadjusted risk difference is -0.051, with a 95% confidence interval from -0.318 to 0.217 and an unadjusted p-value of 0.714. That interval also spans no difference and extends in either direction.

The secondary findings do not resolve the uncertainty in the primary ORR comparison. Disease control is related to response but has a different endpoint definition, while survival and duration outcomes address different aspects of disease course. Agreement or disagreement among these outcomes would not automatically establish or negate the primary result. The registry record lists other secondary outcomes, but their numerical results are not included in the registry record for this interpretation.

Secondary outcomes often involve multiple comparisons. When many endpoints are examined, the chance of seeing an apparently notable result by chance can increase unless the analysis accounts for multiplicity. The registry record does not report whether multiplicity adjustments or a hierarchy for secondary endpoints were specified. The unadjusted disease-control p-value should therefore be treated as descriptive rather than as confirmatory evidence. More broadly, secondary results provide context and may generate questions, but they carry less weight for a firm claim when their testing strategy and adjustment procedures are not reported.

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

• Progression-free Survival (PFS) After Randomization
• Overall Survival (OS) After Randomization
• OS Rates at Specified Timepoints
• Duration of Response (DOR)
• Disease Control Rate (DCR)
• Number of Participants With Adverse Events (AEs)

9. Statistical Interpretation

10. Statistical Methods Explained

Objective response is a binary endpoint: a participant either meets the response definition or does not. The registry presents the outcome as a percentage of participants, with a 95% confidence interval. This makes it possible to consider both the observed response rate and the uncertainty around that estimate. The percentage is a compact description of the observed group, while the interval indicates that the underlying response rate is not known exactly.

What does the arm comparison estimate?

The recalculated comparison uses the observed response proportions in the two arms to estimate a risk difference. A risk difference expresses the absolute contrast between two event proportions on the probability scale. A value of zero would correspond to no difference in the proportions. Negative values in the comparison as defined indicate a lower response proportion in the Atezo + CAPOX + Tira arm than in the Atezo + CAPOX arm. The recalculated estimate is unadjusted: it compares the posted summary results without adjustment for other variables.

A confidence interval for a risk difference describes a range of values compatible with the data under the calculation’s assumptions. If it spans zero, the results do not rule out no difference at the confidence level used. It may also include differences in either direction. An interval crossing zero is not evidence that the arms are identical; it indicates that these data do not resolve the direction and size of the difference with precision.

What does the p-value say?

The unadjusted p-value of 0.356 is a measure of how unusual results at least as far from the no-difference value would be under a statistical model that assumes no true difference. It is not the probability that the null hypothesis is true, and it does not measure the probability that a treatment works. A p-value also does not describe the size or clinical importance of a contrast. In this case, it should be read alongside the estimated difference and its confidence interval rather than as a stand-alone verdict.

The registry’s sponsor-reported analysis states a difference in overall response rates and a 95% confidence interval, but does not list a p-value. The recalculated unadjusted analysis and sponsor-reported analysis are different presentations of the comparison. The record does not report enough detail about the sponsor’s statistical method to reconstruct its interval or assess all of its assumptions.

Why can binary outcomes be over-dispersed?

For a binary endpoint, simple calculations often rely on a model in which participants’ outcomes behave independently and the event probability is sufficiently represented by the observed group proportion. In practice, response chances may vary across participants because of differences in prognosis, disease features, treatment exposure, or assessment circumstances. Such heterogeneity can make outcomes more variable than a simple model expects; this is commonly described as over-dispersion. If present, extra variability can make confidence intervals too narrow and tests too optimistic when ignored.

The registry record does not report a specific assessment or adjustment for over-dispersion. This is a general statistical consideration, not a claim that over-dispersion was demonstrated in this study. Small groups make the results particularly sensitive to how individual outcomes are distributed and to the method used to calculate an interval.

How should the response definition be understood?

The endpoint requires a qualifying complete or partial response on two consecutive assessments at least four weeks apart. This confirmation requirement distinguishes the endpoint from a one-time observation of shrinkage. The investigator applied RECIST v1.1. Missing or absent response assessments were classified as non-responses, and the efficacy-evaluable population required receipt of at least one dose of each drug in the assigned regimen. These definitions determine which observations contribute to the posted rates and how unobserved outcomes are classified.

The registry lists secondary outcomes including progression-free survival, overall survival, survival rates at specified timepoints, duration of response, disease control rate, and adverse events. Each addresses a different aspect of outcome and has different statistical considerations. The record does not provide the analysis methods for those outcomes in the registry record for this explanation, so no assumptions should be made about censoring rules, time-to-event models, or covariate adjustment.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate locates the value that could plausibly apply beyond the observed participants under the analysis assumptions. For the primary endpoint, the arm-specific 95% confidence intervals are 30.76 to 78.47 for Atezo + CAPOX and 20.71 to 63.65 for Atezo + CAPOX + Tira. Both intervals are broad, reflecting substantial uncertainty around the response percentages.

The recalculated risk-difference interval runs from -0.455 to 0.162. It includes zero, as well as values below and above zero, so the data do not determine the direction of the underlying difference with precision. The sponsor reports a 95% interval for the difference in overall response rates from -50.50 to 21.21. The sponsor’s point estimate is -14.65. The registry does not report the sponsor’s p-value or the calculation method behind that interval.

Confidence intervals are not guarantees that a particular range contains the true value, nor are they a range of individual participant outcomes. They communicate uncertainty under the method used to construct them. Their interpretation depends on the analysis assumptions, which are not fully described in the registry record. With small arm sizes, each participant’s response classification can have a notable influence on the group percentage, and the resulting intervals can remain wide.

The interval should therefore temper any reading of the point estimates as stable or exact. The results leave room for meaningfully different underlying response rates in either direction. This is a statement about statistical precision, not a judgment about the clinical importance of any particular difference.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the study’s original design assumptions. For this binary response outcome, the figures are participants per arm, not total event counts. The 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 are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column expresses the analogous planning target for a 90% chance. Higher target power generally requires a larger planned sample for the same effect and assumptions.

The rows labeled 100%, 75%, and 50% of the observed effect illustrate how the planning result changes when the target effect is smaller than the observed estimate. For 100% of the observed effect, the figures are 182 participants per arm for 80% power and 243 participants per arm for 90% power. For 75% of the observed effect, they are 325 and 434 participants per arm. For 50% of the observed effect, they are 730 and 977 participants per arm. Smaller effects need more participants to detect under the stated planning assumptions.

These are planning illustrations, not observed power. They do not indicate the chance that the study’s observed result is true, and they do not establish what the original trial was designed to detect. Because they use the observed effect as their starting point, they should be read as conditional planning scenarios rather than as an explanation of the trial’s enrollment or termination.

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 = 0.556; treatment proportion p₁ = 0.409; average p̄ = 0.482.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7067 = 1.3850.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6990 = 0.5883.
4. n = (1.3850 + 0.5883)² / (-0.1465)² = 181.5, rounded up to 182 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 <- 0.555555555555556                          # control proportion
p1 <- 0.409090909090909                          # 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(5251948)
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 = 182 (80% power), 243 (90% power)
 75% of observed effect: n per arm = 325 (80% power), 434 (90% power)
 50% of observed effect: n per arm = 730 (80% power), 977 (90% power)
power.prop.test: 181.5 
Simulated power at n = 182 per arm: 0.808 (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 own reported analysis gives a difference in overall response rates of -14.65, with a 95% confidence interval from -50.50 to 21.21. The registry does not report a p-value for that analysis. Its point estimate is consistent in direction with the arm percentages: the observed response percentage was lower in Atezo + CAPOX + Tira than in Atezo + CAPOX.

The unadjusted recalculation from the posted group summaries gives a risk difference of -0.146, with a 95% confidence interval from -0.455 to 0.162 and an unadjusted p-value of 0.356. The recalculation is a simple comparison of posted summary statistics; it is not a substitute for a fully specified analysis model. The record does not report the sponsor’s method in sufficient detail to explain the difference between the two confidence intervals.

The sponsor’s reported estimate should be read as the analysis reported by the study sponsor, while the recalculation is a separate, unadjusted check. Neither presentation makes the interval narrow: both include values on both sides of no difference. The registry record does not identify a reason to prefer one interval based on methodological details, so the comparison should be interpreted with that limitation in mind.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several endpoints, comparisons, timepoints, or treatment arms. The more statistical questions examined, the greater the possibility that some result will appear noteworthy by chance, even when the underlying effects are absent. Methods such as prespecified testing hierarchies or adjusted significance thresholds can control this risk, but the registry record does not report whether such methods were planned or used.

The study is an umbrella design that can open new arms, close existing ones, and modify the participant population. This flexibility is part of the design described in the record, but it also makes it important to know which comparisons and analyses were prespecified, when decisions were made, and how results across arms were handled. Those details are not reported in the registry record. Interim analyses and rules for stopping or modifying arms are also not reported in the registry record; the general flexibility described for the study does not establish that any particular interim analysis occurred.

For the primary outcome, the record specifies that missing or absent response assessments were classified as non-responders. It also defines the efficacy-evaluable population as participants who received at least one dose of each drug in their assigned regimen. The registry does not provide enough detail to assess how that population relates to all randomized participants, how many participants were excluded from the efficacy analysis, or how other missing data were handled for secondary outcomes.

The record does not report the protocol’s original sample-size justification, its full statistical analysis plan, whether the analysis was intention-to-treat, or the criteria used to define analysis populations beyond the primary endpoint description. These omissions do not invalidate the reported rates, but they limit evaluation of whether all planned outcomes and comparisons were analyzed as intended and whether the reported results should be considered confirmatory.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (9.1%), anaemia (5.6%), acute coronary syndrome (5.6%), small intestinal obstruction (5.6%), autoimmune hepatitis (5.6%).

The safety results report serious adverse events in 9 of 18 participants in the Atezo + CAPOX arm and 12 of 22 participants in the Atezo + CAPOX + Tira arm. Other adverse events are reported for 18 of 18 and 22 of 22 participants, respectively. Deaths are listed for 13 participants in the first arm and 18 in the second. These are counts in the registry’s safety results; the record does not establish that every reported event or death was caused by study treatment.

The registry lists pneumonia at 9.1% and anaemia, acute coronary syndrome, small intestinal obstruction, autoimmune hepatitis, and jaundice at 5.6% each among the top serious adverse event terms. These summaries describe reported event categories and do not, on their own, convey event timing, severity beyond the serious classification, duration, recurrence, or causal attribution. The registry record does not report those details in the registry record.

Safety counts should be interpreted with the size and exposure of each group in mind. They are descriptive and do not establish a comparative safety profile. The record does not report the statistical methods used for a formal safety comparison.

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

The posted results describe objective response among efficacy-evaluable participants in two Stage 1 treatment arms. The observed ORR was 55.6% for Atezo + CAPOX and 40.9% for Atezo + CAPOX + Tira. The numerical contrast favors the former arm, while the confidence intervals and unadjusted comparison show substantial uncertainty about the underlying difference. The results do not establish that the arms are the same, or that one is superior.

These outcomes should not be interpreted as a direct measure of survival, duration of response, quality of life, or long-term disease control. The registry lists some of these as secondary outcomes, but the numerical results needed to assess them are not included in the registry record for this interpretation. ORR captures a defined response status during Stage 1; it cannot answer every question about the course of disease or the balance of benefits and harms.

The comparison also does not isolate the effect of adding tiragolumab in all possible settings. It compares the two posted regimens in this study’s eligible population and analysis framework. The open-label design, investigator assessment, limited size of the posted arms, and unreported details of the analysis plan should be considered when interpreting the contrast.

The study’s terminated status is a registry fact, but the reason for termination is not reported in the registry record. It would be inappropriate to infer from status alone that the trial stopped because of efficacy, safety, recruitment, or any other particular cause. The results are best understood as the posted evidence for the defined endpoint and population, with substantial uncertainty and important gaps in the registry’s account of study conduct and analysis.

18. Why This Trial Matters Statistically

This study illustrates several statistical issues that arise in randomized umbrella trials. Multiple treatment arms and the possibility of future arm changes can make the scope of a comparison less fixed than in a simple two-arm study. Clear reporting of which arms were active, how comparisons were selected, and how multiplicity was handled is essential for readers to distinguish planned analyses from exploratory ones. The registry describes a flexible design but does not report these analysis details.

It also shows why an observed percentage should not be interpreted without its uncertainty. The ORR estimates differ numerically, but the confidence intervals are broad and the comparison interval includes no difference. A point estimate describes the observed sample; precision indicates how much confidence to place in its value as an estimate of a broader treatment effect.

The endpoint definition matters as well. Requiring confirmation of response, using investigator assessment, and classifying missing or absent assessments as non-responses all shape the meaning of the reported rate. Those rules are not merely technical details: they determine what counts as a response and how participants without an observed response are treated analytically.

Finally, planning illustrations based on an observed effect are not evidence of what the original design assumed or of the study’s achieved statistical power. Keeping planning calculations, sponsor-reported estimates, and unadjusted recalculations distinct helps prevent a descriptive registry result from being overinterpreted. These are broadly useful principles for reading early-phase randomized comparisons, especially when reporting about analysis plans and trial decisions is incomplete.

19. Limitations

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

The posted primary comparison involves relatively small arm sizes, with 18 participants in Atezo + CAPOX and 22 in Atezo + CAPOX + Tira. The resulting response estimates have broad confidence intervals, so the true arm-specific response rates and their difference remain uncertain. Small group sizes also mean that individual response classifications can have a visible effect on the estimates.

The trial was open-label, and the primary endpoint was determined by the investigator. The registry does not report whether response assessment was independently reviewed or whether procedures were used to reduce potential assessment bias. Randomization is reported, but details such as allocation concealment and stratification are not included in the record details.

The umbrella design allowed arms and the participant population to change. The registry record does not provide a detailed account of how those changes occurred, which comparisons were prespecified, or whether analyses were adjusted for the range of outcomes and comparisons. The reason for the terminated status is not reported in the registry record. This limits interpretation of the study’s operational context.

The primary outcome uses an efficacy-evaluable population defined by receipt of at least one dose of each assigned drug, and missing or absent response assessments were classified as non-responders. The available information does not show how many randomized participants were outside that population or provide a complete account of missing data across outcomes. The sponsor’s analysis method is also not described in enough detail to explain its confidence interval. These limitations do not change the reported numbers, but they constrain how confidently the results can be generalized or compared with other evidence.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: An Umbrella Study Evaluating the Efficacy and Safety of Multiple Treatment Combinations in Patients With Gastric or Gastroesophageal Junction Carcinoma — NCT05251948.
• Registry record last updated 2026-04-15; status last verified 2026-04.
• Results first posted 2026-04-15.
• 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

NCT05251948 is a Phase Ib/II, randomized, open-label, multicenter umbrella study in gastric or gastroesophageal junction carcinoma. The registry lists enrollment of 40 and status as terminated. The two posted Stage 1 arms are Atezo + CAPOX and Atezo + CAPOX + Tira.

The primary endpoint is investigator-assessed ORR according to RECIST v1.1, with response confirmation on consecutive assessments at least four weeks apart. The reported response rates are 55.6% and 40.9%, respectively. The unadjusted recalculation gives a risk difference of -0.146, with a 95% confidence interval from -0.455 to 0.162 and p = 0.356. The sponsor reports a difference of -14.65 with a 95% confidence interval from -50.50 to 21.21.

The confidence intervals are broad and include no difference. The registry record does not report the reason for termination, the original sample-size rationale, or a full statistical analysis plan.