A Study of Herceptin (Trastuzumab) in Combination With Cisplatin/Capecitabine Chemotherapy in Participants With Human Epidermal Growth Factor Receptor 2 (HER2)-Positive Metastatic Gastric or Gastro-Esophageal Junction Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Herceptin (Trastuzumab) in Combination With Cisplatin/Capecitabine Chemotherapy in Participants With Human Epidermal Growth Factor Receptor 2 (HER2)-Positive Metastatic Gastric or Gastro-Esophageal Junction Cancer (NCT01450696), a randomized phase 3 study. The primary outcome is Percentage of Participants Who Died - FAS.

2. Clinical Question

The trial therefore addresses a regimen comparison rather than a comparison of trastuzumab plus chemotherapy against no trastuzumab or against a different chemotherapy combination. The background chemotherapy was shared across the groups, while the trastuzumab maintenance dose differed. The stated primary outcome is a percentage of participants who died, not a median survival time or a time-to-event hazard ratio.

The record describes the study as international, multicenter, randomized, open label, and Phase IIIb. The title identifies metastatic gastric or gastro-esophageal junction adenocarcinoma, while the condition field lists Gastric Cancer. These details define the registry’s stated scope; they do not establish how broadly the results apply beyond the enrolled and evaluable participants.

3. Trial Design

The registry record describes a randomized, open-label, parallel-group Phase IIIb study. Its official title identifies a comparison of two trastuzumab dosing regimens, each combined with cisplatin and capecitabine as first-line therapy for HER2-positive metastatic gastric or gastro-esophageal junction adenocarcinoma in participants without prior treatment for metastatic disease. The study was multicenter and international, and masking was not used. Enrollment is listed as 296.

Both groups received trastuzumab as an 8 mg/kg loading dose, followed by a different dose every 3 weeks: 6 mg/kg in one group and 10 mg/kg in the other. The registry describes the 6 mg/kg regimen as standard of care. Capecitabine was planned for 6 cycles at 800 mg/m^2 orally twice a day on Days 1 to 14 of each 3-week cycle. Cisplatin was planned for 6 cycles at 80 mg/m^2 on Day 1 of each 3-week cycle. Trastuzumab was to continue until disease progression; the arm descriptions also list unacceptable toxicity or withdrawal for another reason as stopping circumstances.

The registry lists a start in 2011-12 and primary completion in 2015-02. The study status is terminated. The reason for termination is not reported in the registry record. The record does not report the trial’s original sample-size justification or the design assumptions used when planning the randomized comparison. Those omissions mean the listed enrollment and posted outcome counts should not be treated as evidence of the rationale for the original design.

The primary outcome analysis is described for the FAS population and uses participants evaluable for the outcome. Other reported outcomes use the PPS for some clinical endpoints and the FAS for trastuzumab concentration outcomes. These populations are not interchangeable: an estimate applies to the population and evaluability definition attached to that endpoint, rather than automatically to every randomized participant.

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: A total of 248 participants (124 participants per arm) were randomized in the study up to data cutoff date of 13 February 2015, and 48 additional participants (24 participants per arm) were randomized between data cutoff date of 13 February 2015 and end of study (25 August 2015) for additional safety data.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS population. Here, number of participants analyzed reflects the number of participants who were evaluable for this outcome measure.

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: The Full Analysis Set (FAS) population included all participants who were randomized in this study.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Died - FAS, measured over From date of randomization until death or premature withdrawal (up to approximately 31 months or data cutoff date of 13 February 2015).

The primary endpoint is the percentage of participants who died as of the analysis data cutoff date of 13 February 2015. The specified time frame begins at randomization and continues until death or premature withdrawal, up to approximately 31 months or the data cutoff. The registry says the percentage was reported among participants in the FAS with available data. For this measure, the analyzed number reflects those evaluable for the outcome.

A percentage of participants who died is a binary-outcome summary: each participant is classified according to whether the event was recorded by the specified cutoff. It gives a direct description of event frequency in each group, but it does not by itself describe when deaths occurred. It also does not provide the same information as a survival curve or a hazard ratio, which use time-to-event information.

This endpoint is useful for comparing the observed event proportions under the two randomized regimens at the stated analysis cutoff. Its interpretation depends on the cutoff, follow-up, and availability of outcome data. Participants who had not died by the cutoff are not necessarily known to remain alive indefinitely; the endpoint is a snapshot at the analysis time. Premature withdrawal and missing outcome data can also affect which participants contribute to the reported percentages. The registry does not report a detailed missing-data method for this endpoint.

The posted percentages are descriptive estimates for the evaluable FAS participants. The unadjusted comparison adds an estimate of the risk difference and a confidence interval, which indicate the range of differences compatible with the posted summary data under that calculation. This does not replace the sponsor’s full analysis plan, which is not reported in the registry record.

7. Results Posted in the Registry

• Capecitabine + Cisplatin + Herceptin (10 mg/kg): 54.0% (67/124) versus 46.8% (58/124) on control; risk difference 7.3 percentage points (95% CI -5.2 to 19.7), risk ratio 1.16 (0.90–1.48); unadjusted two-proportion z-test p = 0.253.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants Who Died - Per Protocol Set (PPS)

• 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:
  • Capecitabine + Cisplatin + Herceptin (10 mg/kg): 59.4% (19/32) versus 51.5% (17/33) on control; risk difference 7.9 percentage points (95% CI -16.2 to 31.9), risk ratio 1.15 (0.74–1.79); unadjusted two-proportion z-test p = 0.524.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Capecitabine + Cisplatin + Herceptin (10 mg/kg) and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival - PPS

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Capecitabine + Cisplatin + Herceptin (6 mg/kg) vs Capecitabine + Cisplatin + Herceptin (10 mg/kg): hazard ratio 1.00 (95% CI 0.49–2.04), reported p = 0.993 (as reported in the registry).
  • Capecitabine + Cisplatin + Herceptin (6 mg/kg) vs Capecitabine + Cisplatin + Herceptin (10 mg/kg): hazard ratio 1.02 (95% CI 0.52–2.02), reported p = 0.946 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Capecitabine + Cisplatin + Herceptin (6 mg/kg) vs Capecitabine + Cisplatin + Herceptin (10 mg/kg) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Capecitabine + Cisplatin + Herceptin (6 mg/kg) vs Capecitabine + Cisplatin + Herceptin (10 mg/kg) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Disease Progression or Death - PPS

• 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:
  • Capecitabine + Cisplatin + Herceptin (10 mg/kg): 81.2% (26/32) versus 75.8% (25/33) on control; risk difference 5.5 percentage points (95% CI -14.4 to 25.4), risk ratio 1.07 (0.83–1.38); unadjusted two-proportion z-test p = 0.590.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Capecitabine + Cisplatin + Herceptin (10 mg/kg) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover mortality, overall survival, progression or death, progression-free survival, objective response, and trastuzumab concentrations. They broaden the description of the trial beyond the primary death percentage, but they do not all measure the same clinical feature. Some are event proportions, some are time-to-event outcomes, and the concentration outcomes are pharmacokinetic measures. The registry lists 7 secondary outcomes, while the posted results include different levels of detail across outcomes.

The mortality and progression-or-death percentages in the PPS point in the same numerical direction as the primary FAS percentages, with higher reported event percentages in the 10 mg/kg group. The overall-survival records do not show a clear separation by their reported hazard-ratio analyses, and the confidence intervals are broad. This overall pattern is not a coherent body of precise evidence favoring one regimen; it reflects estimates with meaningful uncertainty and analysis populations that vary by endpoint. The secondary findings do not override or independently confirm the primary result.

Secondary outcomes often have less inferential weight than a primary endpoint because they may be numerous, exploratory, or assessed in populations and ways that differ from the primary analysis. Testing multiple outcomes increases the chance of apparently notable results arising by chance if no adjustment or hierarchy is used. The registry record does not report a multiplicity-control strategy for these secondary analyses. Their p-values, where reported, should therefore not be treated as if each were the sole prespecified test.

Several secondary outcomes are named in the registry but do not have detailed results in the record described. A missing posted estimate is not evidence that the outcome was unchanged or that no events occurred. Nor can an outcome with a favorable-looking point estimate establish a treatment effect on its own when its precision, analysis rules, and relation to the planned testing strategy are unclear. The most responsible reading is to use secondary outcomes as contextual evidence, while giving primary emphasis to the stated primary endpoint and acknowledging the limits of the available analyses.

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

• Percentage of Participants Who Died - Per Protocol Set (PPS)
• Overall Survival - PPS
• Percentage of Participants With Disease Progression or Death - PPS
• Progression-Free Survival - PPS
• Percentage of Participants With Objective Response - PPS
• Trastuzumab Cmin on Day 21 of Cycles 1 to 11 - FAS
• Trastuzumab Serum Concentration on Day 1 of Cycle 1 - FAS

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: for the stated analysis cutoff, a participant either had a recorded death or did not. A group percentage estimates the frequency of that event among the participants evaluable for the endpoint. The observed percentages are therefore easy to understand, but they do not preserve the timing of events. A participant who died early and a participant who died later both contribute to the event percentage, provided each is counted by the cutoff.

What does the risk difference describe?

The unadjusted risk difference compares the event proportion in the 10 mg/kg group with the event proportion in the 6 mg/kg group. Its estimate is 0.073. A positive value means the observed event proportion is higher in the first-named group for this subtraction order; a negative value would mean it is lower. The 95% confidence interval runs from -0.051 to 0.197. Because the interval crosses zero, the summary data are compatible with no difference as well as with differences in either direction. The unadjusted p-value is 0.253. A p-value describes how unusual data at least as discrepant as those observed would be under a specified null model; it is not the probability that the null hypothesis is true, nor a measure of clinical importance.

This risk-difference calculation is labeled a recalculation because it is an unadjusted calculation from posted summary statistics. It is not an assertion that this was the sponsor’s prespecified analysis. The registry’s primary outcome description gives the endpoint and population but does not report the sponsor’s detailed statistical model, adjustment strategy, or prespecified test. When a sponsor analysis is reported, it takes precedence over a simple recalculation; the primary endpoint record does not include such a reported comparison.

How does a confidence interval differ from a p-value?

A confidence interval communicates uncertainty about an estimated effect in the same units as that effect. It presents a range of values compatible with the data and the method used, rather than a single point estimate alone. A p-value compresses evidence against a null hypothesis into a probability calculated under that hypothesis and the model assumptions. Neither quantity answers whether an observed difference is clinically important. The interpretation also depends on how the endpoint was defined, who was included, and whether the analysis was planned in advance.

Why are survival methods different?

Overall survival and progression-free survival are time-to-event outcomes. They account for the time from the stated starting point until an event, while allowing that some participants may not have an observed event during available follow-up. A median survival estimate describes the time by which half of the estimated population has experienced the event under the survival analysis. A hazard ratio compares event rates over time as represented by the model; it is not a ratio of the posted median times or a comparison of simple percentages.

The overall-survival analyses are reported as log-rank hazard ratios with confidence intervals and p-values. The record lists two results for this endpoint but does not explain the reason for the two analyses. The intervals are wide, and each includes the value 1.00, which represents no relative hazard difference under the hazard-ratio scale. These results do not establish equivalence. The registry does not report enough detail to reconstruct the underlying survival curves, censoring patterns, or the reason for each analysis.

What does randomization contribute?

Random allocation is intended to make treatment groups comparable, on average, with respect to factors known and unknown at the time of assignment. It supports a causal comparison when the trial is conducted and analyzed as planned. It does not guarantee that the groups are identical in every feature, and it does not resolve problems caused by missing outcomes, deviations from assigned treatment, or selective reporting. The open-label design means treatment assignment was not masked; the registry does not describe whether outcome assessment or analysis had any separate masking safeguards.

The posted primary group counts are 124 evaluable participants in each arm. The PPS figures for secondary outcomes differ from the FAS figures, reflecting the use of a different analysis population as recorded for those outcomes. A result in the PPS is conditional on inclusion in that set; it should not be read as if it necessarily had the same protection against selection effects as the randomized comparison. The registry does not report detailed rules for entry into the PPS.

Why can outcome percentages differ across analysis sets?

Analysis populations can differ because eligibility, treatment exposure, protocol adherence, evaluability, and data availability are handled differently. These choices affect which observations contribute to an estimate. The primary result is explicitly described as an FAS result among participants with available data, and its analyzed number represents those evaluable for the outcome. The PPS secondary outcomes use a distinct population label. The registry record does not report a complete accounting of every exclusion or missing outcome for each analysis.

These methods explain why a point estimate, its uncertainty, and its analysis population must be read together. General statistical principles do not fill gaps in a registry record: details such as the original sample-size justification, any interim analyses, the complete multiplicity strategy, and the sponsor’s full statistical analysis plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary comparison’s risk-difference estimate is 0.073, with a 95% confidence interval from -0.051 to 0.197. This interval is wide enough to include zero and values on either side of zero. It therefore leaves uncertainty not only about the size of a possible difference but also about its direction. The primary p-value, 0.253, is consistent with the interval’s failure to separate the estimate from zero under the unadjusted calculation.

A confidence interval is a measure of statistical precision, not a guarantee that the true effect lies within the particular interval. In repeated use of the same method under its assumptions, confidence intervals have a long-run coverage interpretation. For an individual study, the practical message is that a range of effects remains compatible with the observed data and calculation. The interval does not account for every possible source of uncertainty, such as unreported analytical choices, missing data, or departures from the assumptions of the method.

The reported overall-survival hazard-ratio intervals are also broad: 0.49 to 2.04 and 0.52 to 2.02. They include 1.00 and encompass materially different relative-hazard values in either direction. The record presents two analyses but does not explain their distinction, so their estimates should be reported as separate registry entries rather than combined or selectively treated as a single definitive result.

Precision is different from clinical importance. A narrow interval can still cover effects too small to matter, while a wide interval can include both important benefit and harm. The registry does not report a threshold for clinical importance or a non-inferiority margin. The evidence should therefore be described in terms of its estimates and uncertainty, without converting lack of statistical separation into proof of equal effects.

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 illustrations based on observed effects, not the trial’s original design calculations. For the binary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column represents the number of participants per arm, or total events for a time-to-event outcome, that the illustration estimates would be needed for an 80% chance of detecting the specified effect under its assumptions. The 90% power column uses a higher target chance of detecting that effect, and therefore generally requires a larger planning figure. These are planning quantities, not counts observed in the trial. They do not describe the probability that the posted finding is true or the probability that this completed study detected an effect.

Rows for 100%, 75%, and 50% of the observed effect explore how the planning quantity changes when the effect to detect is smaller. Smaller effects need more participants or events to detect with the same assumed power and significance level. The observed effect is an unstable basis for future planning, especially when estimated from limited data; the illustration is not a substitute for choosing a clinically meaningful target and specifying an appropriate design.

This is not observed power. It is a forward-looking calculation under stated assumptions, not a retrospective measure of how convincing the results are. Interpretation of the trial should rely on the estimates, confidence intervals, endpoint definitions, and analysis populations rather than on these planning illustrations.

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 = 0.468; treatment proportion p₁ = 0.540; average p̄ = 0.504.
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 × 0.7052 = 0.5935.
4. n = (1.3859 + 0.5935)² / (0.0726)² = 743.7, rounded up to 744 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 <- 0.467741935483871                          # control proportion
p1 <- 0.540322580645161                          # 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(1450696)
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 = 744 (80% power), 996 (90% power)
 75% of observed effect: n per arm = 1,324 (80% power), 1,771 (90% power)
 50% of observed effect: n per arm = 2,977 (80% power), 3,984 (90% power)
power.prop.test: 743.7 
Simulated power at n = 744 per arm: 0.804 (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, analysis population, or statistical comparison. If each test is interpreted independently at a conventional significance threshold, the chance of at least one chance-positive finding can increase across the set of tests. Trial plans commonly address this through a prespecified hierarchy, adjustment, or other strategy, but the registry record does not report the multiplicity strategy for this study. It is therefore not possible to determine from the record whether the posted secondary p-values were adjusted or how they were intended to support confirmatory claims.

The registry lists multiple secondary outcomes and reports more than one overall-survival analysis. It does not explain why the two overall-survival estimates are both included or whether they correspond to separate populations, models, or analytic choices. Without that context, those estimates should remain separate rather than being combined or treated as interchangeable replications. The number of outcome measures and analyses recorded does not itself reveal the planned testing hierarchy.

Missing-data handling is also important. The primary endpoint description says that the percentage was reported among FAS participants with available data and that the analyzed number reflects participants evaluable for the endpoint. The registry does not report the number or reasons for missing primary outcome data, the method used to address missingness, or sensitivity analyses. If availability of data is related to outcome or treatment, a complete-case percentage may not represent the same comparison as a fully observed randomized population. This is a general concern, not evidence that a particular bias occurred in this study.

The FAS and PPS labels define different analysis populations in the registry record. The primary death endpoint is reported in the FAS, while several secondary clinical outcomes are reported in the PPS. Detailed population definitions, exclusions, and adherence rules are not reported in the registry record. Consequently, differences between those results may reflect both outcome and population differences, and should not be attributed solely to the dosing regimen.

The registry also does not report interim-analysis procedures, stopping rules, the original statistical analysis plan, or the original sample-size justification. These missing details limit assessment of whether the reported analyses match the intended confirmatory strategy. The study’s terminated status is recorded, but its reason is not reported in the registry record; no inference about the cause or its effect on the findings is warranted.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anemia (4.8%), vomiting (3.4%), diarrhoea (2.7%), acute kidney injury (2.7%), febrile neutropenia (2.0%).

The registry reports serious adverse event figures for groups described as at risk. In the 6 mg/kg group, 35 of 147 participants at risk had a serious adverse event; in the 10 mg/kg group, 38 of 147 participants at risk had a serious adverse event. For other adverse events, the record lists 123 of 147 at risk in the 6 mg/kg group and 122 of 147 at risk in the 10 mg/kg group. These are separate safety summaries and should not be conflated with the primary mortality endpoint.

The most frequently listed serious adverse event terms include anemia at 4.8%, vomiting at 3.4%, diarrhoea at 2.7%, acute kidney injury at 2.7%, febrile neutropenia at 2.0%, and renal failure at 2.0%. The registry record does not give term-specific group comparisons or confidence intervals for these entries, so they do not establish whether a particular event differed between dosing groups. A serious adverse event count is also not the same as a count of all adverse events, and an individual may experience more than one event.

These figures describe recorded events in the safety population and do not by themselves establish causation or comparative safety. The registry’s adverse-event record should be interpreted alongside the study’s exposure, follow-up, event definitions, and collection methods; detailed information on those features is not reported in the registry record.

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

The posted primary result describes death percentages among FAS participants evaluable for that endpoint by the stated cutoff. It does not show a precise difference between the regimens: the unadjusted risk-difference confidence interval includes zero, and the p-value is 0.253. The result therefore leaves uncertainty about whether a difference exists and, if so, its size and direction. It does not establish that the two regimens are the same.

Likewise, lack of a statistically clear difference is not evidence of equivalence or non-inferiority. Those claims require an appropriate design, a prespecified margin, and analyses aligned with that aim. A non-inferiority margin and formal equivalence strategy are not reported in the registry record. The registry title describes a regimen comparison, but the posted information does not justify replacing uncertainty with a conclusion that either dose is interchangeable with the other.

The observed percentages and secondary estimates are not treatment advice. They are study results for a defined population, regimen comparison, follow-up window, and analysis set. They do not directly answer what would happen in every patient or setting. Generalizability depends on how closely other populations and care settings resemble the trial population and conduct; those questions cannot be settled from the posted summary alone.

The record also does not establish why the study was terminated, whether all planned outcomes were reported, or how missing data and multiple analyses were handled. These gaps matter when interpreting the completeness and confirmatory status of the evidence. The numerical findings should be read as estimates with uncertainty, rather than as proof that a regimen succeeds or fails.

In practical statistical terms, the primary comparison is inconclusive about a difference at the available precision. The secondary results add context but do not remove that uncertainty, particularly because some are based on the PPS and multiple secondary analyses lack a reported multiplicity strategy. The appropriate conclusion is limited to what was observed and posted, with no claim about unreported outcomes or underlying reasons for study conduct.

17. Why This Trial Matters Statistically

This study is statistically informative because it compares two doses of the same biologic treatment while keeping the named chemotherapy combination common to both groups. That design focuses the randomized contrast on the trastuzumab maintenance regimen rather than on the presence or absence of the chemotherapy backbone. It also illustrates why a narrowly targeted question can still yield uncertain estimates when the outcome data and analysis populations are limited.

The primary endpoint is a clinically interpretable event proportion, while several secondary outcomes use time-to-event methods or measure trastuzumab concentrations. Reading these measures together requires attention to what each estimates, when it is assessed, and who contributes data. Percentages cannot substitute for survival analyses, and pharmacokinetic outcomes do not directly answer the same question as clinical outcomes.

The record is also a useful example of the distinction between a trial’s original design and a planning illustration derived from observed effects. The registry reports planning assumptions for an illustration but not the original sample-size justification. That distinction prevents retrospective calculations from being mistaken for evidence that the trial was planned around the effect ultimately observed.

Finally, the primary confidence interval makes uncertainty visible: the point estimate alone would give an incomplete account. The separate PPS analyses, missing multiplicity details, unreported missing-data methods, and unclear reason for termination further show why registry results should be read with careful attention to design and reporting limits. These features do not invalidate the posted estimates, but they constrain the conclusions that can responsibly be drawn from them.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

A key limitation is that the primary endpoint is a percentage by a specified cutoff, not a complete description of time to death. Follow-up is described as up to approximately 31 months or the data cutoff date of 13 February 2015. The registry does not provide detailed follow-up distributions or a full account of censoring and missing outcome data. The primary population includes FAS participants with available data, and the number analyzed is tied to evaluability.

The primary comparison available in the record is an unadjusted recalculation from posted summaries rather than a sponsor-reported adjusted analysis. The registry does not report the full statistical analysis plan, the original sample-size justification, interim analyses, or how multiplicity was addressed. The primary interval is broad, leaving uncertainty about the direction and size of a possible difference.

Secondary clinical outcomes use the PPS, while the primary outcome uses the FAS. The detailed definitions and exclusion rules for these populations are not reported. The overall-survival endpoint has two reported log-rank analyses, with no explanation of their relationship in the registry record. Several listed secondary outcomes do not have detailed results in the record, so their absence cannot be interpreted as absence of events or effects.

The trial is marked terminated, but the reason for termination is not reported in the registry record. The open-label design means assignment was not masked; the record does not describe safeguards for outcome assessment or analysis. The safety summaries provide event counts and selected serious-event terms, but do not provide comparative uncertainty estimates for those terms. These limitations restrict interpretation without establishing that the observed results are biased or unreliable.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Herceptin (Trastuzumab) in Combination With Cisplatin/Capecitabine Chemotherapy in Participants With Human Epidermal Growth Factor Receptor 2 (HER2)-Positive Metastatic Gastric or Gastro-Esophageal Junction Cancer — NCT01450696.
• Registry record last updated 2016-11-28; status last verified 2016-10.
• Results first posted 2016-11-28.
• 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

NCT01450696 is a randomized, open-label, multicenter Phase IIIb study of trastuzumab dosing regimens with cisplatin and capecitabine for HER2-positive metastatic gastric or gastro-esophageal junction adenocarcinoma. The registry lists enrollment of 296 and a terminated status. Participants were assigned to a trastuzumab maintenance dose of 6 mg/kg or 10 mg/kg every 3 weeks after an 8 mg/kg loading dose.

The primary endpoint was the percentage who died by the analysis cutoff, assessed in evaluable FAS participants. The posted percentages were 46.8% and 54.0%; the unadjusted recalculated risk-difference interval includes zero. The record also includes PPS survival and progression outcomes and safety summaries. Important details, including the reason for termination, original design assumptions, multiplicity strategy, and detailed missing-data methods, are not reported in the registry record.