Tislelizumab in Combination With Chemotherapy as First-Line Treatment in Adults With Inoperable, Locally Advanced or Metastatic Gastric, or Gastroesophageal Junction Carcinoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tislelizumab in Combination With Chemotherapy as First-Line Treatment in Adults With Inoperable, Locally Advanced or Metastatic Gastric, or Gastroesophageal Junction Carcinoma (NCT03777657), a randomized phase 3 study. The primary outcome is Overall Survival in PD-L1 Positive Participants.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group phase 3 trial sponsored by BeiGene. The registry record lists triple masking. It describes a first-line comparison in adults with locally advanced unresectable or metastatic gastric or gastroesophageal junction adenocarcinoma. The study status is completed, and the recorded enrollment is 997.

Participants were assigned to tislelizumab plus chemotherapy or placebo plus chemotherapy. Chemotherapy was selected by the investigator and consisted of a platinum and a fluoropyrimidine; the intervention list names cisplatin, oxaliplatin, capecitabine, and 5-fluorouracil. The tislelizumab arm description records 200 mg intravenously once every 3 weeks for up to six cycles. The comparator received intravenous placebo with chemotherapy on the same stated schedule. Further details of the chemotherapy schedules are not fully present in the registry record.

The primary endpoint was overall survival in the PD-L1-positive analysis set. That set included randomized participants whose tumors met the registry's PD-L1-positive definition. For this primary analysis, the posted arm sizes are 274 and 272. The trial also reports results for several secondary outcomes and populations, including progression-free survival and response outcomes. These populations and endpoints are not interchangeable: the PD-L1-positive analysis set is distinct from the intention-to-treat analysis set.

The study began on 2018-12-13. The primary completion date is recorded as 2023-02-28. The primary overall-survival analysis used a data cutoff of 8 October 2021, while the posted final-efficacy progression-free-survival results use a cutoff of 28 February 2023. The reasons for these analysis timings, the randomization procedure in detail, the original sample-size justification, and the precise roles covered by masking are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participants were randomly assigned to either tislelizumab plus investigator chosen chemotherapy (ICC) or placebo plus ICC. Randomization was stratified according to region (China \[including Taiwan\] vs Japan and South Korea vs Europe/North America), programmed cell death protein ligand-1 (PD-L1) expression (PDL1 tumor area positivity (TAP) score ≥5% or \<5%), peritoneal metastases (yes vs no), and investigator's choice of chemotherapy (capecitabine + oxaliplatin, or 5-fluorouracil + cisplatin).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The PD-L1-Positive Analysis Set included all randomized participants whose tumors were PD-L1 positive (defined as PD-L1 TAP score ≥ 5%)

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 Overall Survival in PD-L1 Positive Participants, measured over From randomization up to the primary analysis data cut-off date of 8 October 2021; Median (range) time on follow-up was 11.8 (0.1 - 33.4) months..

Overall survival is the time from randomization to death from any cause. It is a time-to-event endpoint: each participant contributes information until death or, if death has not been observed by the analysis cutoff, until the participant's available follow-up ends. The registry record says median overall survival was estimated with the Kaplan-Meier method.

Overall survival is used because it directly captures the duration participants remain alive, regardless of the particular cause of death. It does not require a judgment that a change in a scan or a symptom represents progression. That direct interpretation comes with practical statistical considerations: participants may still be alive when follow-up is cut off, so their survival time is incomplete rather than a known event time. Kaplan-Meier estimation accommodates this kind of censoring under assumptions about how censoring relates to the event process.

The primary endpoint is restricted to the PD-L1-positive analysis set, not all randomized participants. The posted record defines that population using tumor PD-L1 TAP score. The primary analysis cutoff was 8 October 2021, and median follow-up was reported as 11.8 months, with a range of 0.1 to 33.4 months. These details describe the observation available for the analysis; they do not mean that every participant was followed for the same length of time. The endpoint answers a comparative survival question for the defined analysis population and cutoff, rather than establishing an outcome for every patient with the condition.

7. Results Posted in the Registry

• Tislelizumab + Chemotherapy vs Placebo + Chemotherapy: hazard ratio 0.74 (95% CI 0.59–0.94), reported p = 0.006 (as reported in the registry).

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.

Progression-free Survival (PFS) in PD-L1 Positive Participants

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Tislelizumab + Chemotherapy vs Placebo + Chemotherapy: hazard ratio 0.68 (95% CI 0.56–0.83) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Tislelizumab + Chemotherapy vs Placebo + Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Response Rate (ORR) in PD-L1 Positive Participants

• 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:
  • Tislelizumab + Chemotherapy: 51.5% (141/274) versus 42.6% (116/272) on control; risk difference 8.8 percentage points (95% CI 0.5 to 17.2), risk ratio 1.21 (1.01–1.44); unadjusted two-proportion z-test p = 0.039.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Tislelizumab + Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Progression-free Survival (PFS) in the ITT Analysis Set

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Tislelizumab + Chemotherapy vs Placebo + Chemotherapy: hazard ratio 0.78 (95% CI 0.67–0.90) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Tislelizumab + Chemotherapy vs Placebo + Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results provide context around the primary overall-survival comparison, but they address related rather than identical outcomes. The PD-L1-positive progression-free-survival result and the intention-to-treat progression-free-survival result point in the same general direction as the primary result. The PD-L1-positive response outcome also has a higher posted response proportion in the tislelizumab-plus-chemotherapy arm. Taken together, the available numerical pattern is directionally consistent across these posted comparisons.

That consistency should not be mistaken for a set of independent confirmations. Progression-free survival, response, and overall survival measure different aspects of outcome, and some analyses use overlapping participants. The PD-L1-positive and intention-to-treat sets also differ. Secondary estimates can support a broader descriptive understanding, but they do not change the definition or population of the primary endpoint.

The posted secondary hazard-ratio comparisons do not include p-values in the registry record. Several secondary outcomes and analysis populations are listed, and the record does not report a multiplicity adjustment or a hierarchy showing which comparisons were confirmatory. When many outcomes are examined, the chance of finding at least one apparently notable result by chance can increase. This general concern means that unadjusted secondary results carry less inferential weight than a prespecified primary result whose testing approach is defined. The registry record does not establish how these secondary outcomes were intended to be classified.

The secondary tables are best read for their estimates, uncertainty, populations, and endpoint definitions rather than as a checklist of positive or negative findings. No conclusion about unlisted secondary estimates should be inferred from the outcomes named in the record. Other secondary results, including quality-of-life outcomes, are listed, but their numerical results are not included in the registry record.

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

• Progression-free Survival (PFS) in PD-L1 Positive Participants
• Overall Response Rate (ORR) in PD-L1 Positive Participants
• Progression-free Survival (PFS) in the ITT Analysis Set
• Overall Response Rate (ORR) in the ITT Analysis Set
• Duration of Response (DOR) in PD-L1 Positive Participants
• Duration of Response in the ITT Analysis Set
• Change From Baseline in European Organization for Research and Treatment of Cancer (EORTC) Quality of Life Questionnaire-Core 30 (QLQ-C30) Global Health Status (GHS)/Quality of Life (QOL) and Physical Functioning Scores
• Change From Baseline in EORTC QLQ-C30 Fatigue Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. The event is death from any cause, and the time origin is randomization. Some participants may not have had a death recorded by the analysis cutoff. In general, such observations are censored at the last available point at which survival status is known. The record defines the endpoint and cutoff but does not describe the censoring rules or missing-data procedures in detail.

Kaplan-Meier estimation

The registry record says median overall survival was estimated with the Kaplan-Meier method. In general, this method estimates the proportion surviving over time while accounting for participants whose event time is censored. It uses the event times and the number still under observation at those times, rather than treating everyone as if they had identical follow-up. The estimated median is the point at which the estimated survival function reaches one half, if that point is observed. A median summarizes one location on the survival curve; it does not describe the whole curve or the survival experience at every time.

Hazard ratios and the log-rank test

The reported primary comparison is a hazard ratio, with a 95% confidence interval, and the named test is a one-sided log-rank test. In general, a hazard is the instantaneous event rate among participants who have not yet experienced the event. A hazard ratio compares those rates between groups over the analysis period. A value below 1 is in the direction of a lower event hazard in the tislelizumab-plus-chemotherapy group, as labelled in the comparison. It is not a direct comparison of median survival, and its interpretation as a single summary can be less straightforward if the relative hazards change over time.

The log-rank test compares the observed and expected event experience between groups over follow-up. The registry record identifies this as a one-sided test for the primary comparison and reports its p-value. A one-sided test evaluates evidence in a prespecified direction, but the basis for choosing that direction and the full testing plan are not reported in the registry record. The reported p-value should therefore be understood as the result of the named test, not as a measure of effect size or as the probability that the null hypothesis is true.

Confidence intervals

A confidence interval conveys statistical uncertainty around an estimate under the analysis method. In general, a 95% confidence interval is generated by a procedure that, under its assumptions, would cover the target parameter in 95% of repeated applications. It is not a statement that there is a 95% probability that this particular interval contains the true value. The primary interval is reported for the hazard ratio. Its width reflects uncertainty in the estimated comparison, but does not address possible bias from outcome assessment, missingness, choice of analysis population, or other design and conduct issues.

Different endpoints and analysis sets

Progression-free survival is another time-to-event endpoint, while overall response rate is a binary response outcome. They answer different questions and use different statistical summaries. A hazard ratio for progression-free survival concerns the event-time comparison specified for that endpoint; an odds ratio for response concerns the odds of response. These measures cannot be read as if they were the same quantity. The PD-L1-positive results and the intention-to-treat results also answer questions in different analysis populations. An estimate in one set does not automatically establish the same effect in another.

For the posted response comparison, the registry includes an odds ratio from the reported analysis. A separate unadjusted calculation from the posted response counts can yield a different estimate or uncertainty because it uses a simple comparison of summary data rather than necessarily reproducing the sponsor's analysis. General statistical practice gives the sponsor's own analysis precedence when the posted results are not discrepant; the registry record does not flag a discrepancy. Differences between methods should not be interpreted as contradictory without understanding their estimands and assumptions.

Over-dispersion and outcome variation

Over-dispersion is a general concern for count outcomes when observed variation exceeds what a simple statistical model expects. It can make standard errors too small if the extra variability is ignored. The primary endpoint is time to death, and the registry describes a log-rank comparison rather than a count model. Over-dispersion is therefore not a basis for reinterpreting the posted primary result. The registry record does not report a separate assessment of over-dispersion for other outcomes.

Limits of what is documented

The registry record does not report the detailed statistical analysis plan, any covariate adjustment, the proportional-hazards assessment, the handling of missing data, interim analyses, or the original sample-size justification. It also does not describe a multiplicity procedure for the multiple endpoints and analysis populations. These omissions do not show that such procedures were absent; they mean that they cannot be evaluated from this record. The reported primary model and test should be distinguished from these unreported design and analysis details.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.74, and its 95% confidence interval runs from 0.59 to 0.94. In plain terms, the interval expresses the range of values reasonably compatible with the data and the stated analysis procedure, subject to its assumptions. Because the interval is entirely below 1, the values it contains are in the direction of a lower event hazard in the tislelizumab-plus-chemotherapy group. The interval nevertheless allows a range of possible effect magnitudes; it does not identify one exact effect.

The reported medians also have confidence intervals: 13.9 to 21.3 months for the tislelizumab group and 12.0 to 14.4 months for the placebo group. These intervals describe uncertainty in each arm's median, whereas the hazard-ratio interval describes uncertainty in the between-group comparison. Overlap or non-overlap of separate arm intervals is not a substitute for the confidence interval or test for the treatment contrast. The analysis uses the survival data across follow-up, not simply a comparison of the two median estimates.

Precision depends on the number and timing of observed events, the amount and distribution of follow-up, and the statistical method. The primary analysis had median follow-up of 11.8 months, with a range of 0.1 to 33.4 months. Participants did not all contribute the same duration of observation. The interval therefore cannot be understood as if every participant had complete, equal follow-up.

Confidence intervals quantify sampling uncertainty under the analysis; they do not account for every source of uncertainty. They do not resolve questions about generalizability beyond the PD-L1-positive set, the implications of using a one-sided test, unreported multiplicity handling, or missing-data methods. The registry record does not report the proportional-hazards assessment, which would help evaluate whether a single hazard ratio is an adequate summary over time. Thus, the interval is useful evidence about statistical precision, but it is not a complete assessment of the result's robustness or practical importance.

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 table and curve are planning illustrations based on the observed effect, not a reconstruction of the trial's original design. For time-to-event outcomes, the displayed figures are total events required, not participants per arm. For other outcomes, the figures are participants per arm. Read the unit for the particular endpoint before comparing figures across sections.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. For time-to-event planning, the calculation uses the Schoenfeld approach. The original trial's own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of events or participants needed for a design with an 80% chance of detecting the assumed effect under those planning assumptions, if that assumed effect were the true effect. The 90% power column describes the corresponding target for a 90% chance. These are prospective design concepts, not statements about how likely the trial was to succeed after seeing its data.

Rows that plan for a smaller fraction of the observed effect require more information, because smaller effects are harder to distinguish from random variation. For time-to-event outcomes, that usually means more events; for other endpoints, it means more participants in each arm. The values are not observed power. They are planning illustrations that help show how the required information changes with the effect being targeted and the chosen power target.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.740, so ln(HR) = -0.3011.
2. d = 4 × (1.96 + 0.842)² / [ln(0.740)]² = 346.3, rounded up to 347 events in total 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
hr <- 0.74                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(3777657)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 347 (80% power), 464 (90% power)
 75% of observed effect: events = 616 (80% power), 825 (90% power)
 50% of observed effect: events = 1,386 (80% power), 1,855 (90% power)
Simulated power with 347 events: 0.808 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 611 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 997 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 12.6          # control-arm median, months (converted from the posted unit)
hr          <- 0.74          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 482         p (1-sided)   0.0001
 Events: 156        ~HR at bound   0.5519
   Month: 19    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.74   0.0338
   IA 2: 67%                   Z   2.5114
      N: 612         p (1-sided)   0.0060
 Events: 312        ~HR at bound   0.7524
   Month: 30    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.74   0.5603
       Final                   Z   1.9930
      N: 612         p (1-sided)   0.0231
 Events: 468        ~HR at bound   0.8317
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.74   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The primary result is the sponsor's reported analysis: a hazard ratio of 0.74, a 95% confidence interval from 0.59 to 0.94, and a one-sided log-rank p-value of 0.006. The posted result identifies the PD-L1-positive population and the primary analysis cutoff. The registry record does not flag a discrepancy between the sponsor's result and the displayed primary result.

Any simple recalculation from posted summary statistics is not a replacement for the sponsor's analysis. A recalculation may use only arm-level counts or summary values and may not reproduce the sponsor's time-to-event methods, censoring information, or analysis set exactly. The sponsor's own analysis takes precedence when a discrepancy is present; no such discrepancy is flagged for this record. For the response outcome, the sponsor reports an odds ratio, whereas an unadjusted calculation from the posted counts is a distinct analysis. Those estimates should be identified by method rather than treated as interchangeable.

The registry record does not provide the full analysis code or detailed statistical analysis plan, so independent reproduction of every part of the sponsor's analysis is not possible from the posted summary alone. The tables and figures should be read as presentations of the registry results, not as evidence that all underlying calculations have been independently reconstructed.

16. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and a broad set of secondary outcomes, including survival, progression-free survival, response, duration of response, and quality-of-life measures. It does not report how the study addressed multiplicity: the possibility that testing several outcomes or populations increases the chance of at least one result appearing statistically notable by chance. It is not reported in the registry record whether a formal adjustment, testing hierarchy, or other strategy was used.

The primary analysis reports a one-sided log-rank test and a p-value. The record does not say whether interim analyses were conducted, whether any interim testing boundaries were used, or how an interim analysis might have affected the final test. These details should not be guessed from the reported p-value or the data cutoff.

Missing-data and censoring procedures are also not described in detail. For survival analyses, participants without a recorded death by the cutoff can contribute censored follow-up; assumptions about censoring matter to interpretation. The record defines the endpoint and gives the cutoff and follow-up summary, but does not explain the specific censoring rules, missing assessments, or sensitivity analyses. For response and quality-of-life outcomes, the registry record does not provide enough information to assess the handling of missing assessments.

The analysis populations are specified for the primary endpoint and some secondary outcomes. The primary analysis set includes randomized participants meeting the PD-L1-positive tumor definition, while some secondary results use the intention-to-treat set. The registry record does not report a full accounting of participant exclusions or the handling of participants without an available biomarker result. These are relevant distinctions when judging how broadly each estimate applies.

These are limits of documentation in the registry record, not proof that the trial did not have a prespecified analysis plan or procedures for missingness and multiplicity. Without those details, the posted estimates can be described, but some aspects of confirmatory interpretation and robustness cannot be assessed.

17. 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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: platelet count decreased (3.4%), pneumonia (2.8%), anaemia (2.0%), death (2.0%), upper gastrointestinal haemorrhage (1.4%).

The posted safety figures count participants with at least one serious adverse event and those with other adverse events, using safety populations of 498 in the tislelizumab-plus-chemotherapy group and 494 in the placebo-plus-chemotherapy group. The record reports serious adverse events in 211 participants in the tislelizumab group and 179 in the placebo group. Other adverse events were reported in 489 and 485 participants, respectively. These are participant counts, not event totals; a participant may experience more than one event.

The record also lists deaths in each group, but the figures alone do not establish their timing, cause, relationship to treatment, or whether a death was counted as an adverse event. Those details are not reported. The most frequently listed serious adverse-event terms include decreased platelet count, pneumonia, anaemia, death, upper gastrointestinal haemorrhage, and general physical health deterioration; the posted percentages describe those terms in the registry record.

These summaries do not establish that a treatment caused an event, and the counts should not be interpreted as a complete individual risk profile. Safety comparisons depend on definitions, observation time, event attribution, and exposure, details that are not fully described in the record. The figures are descriptive trial data and are not medical advice.

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

The primary result shows that, in the PD-L1-positive analysis set and at the recorded primary cutoff, the sponsor's survival comparison favored the tislelizumab-plus-chemotherapy group on the reported hazard-ratio scale. The confidence interval and p-value describe the statistical evidence and uncertainty under the stated analysis. The posted medians offer a second summary of the observed survival experience, but neither the medians nor the hazard ratio gives a certain prediction for an individual.

The finding applies most directly to participants who met the trial's recorded eligibility and PD-L1-positive analysis definition and received the compared first-line regimens in this study. It does not automatically answer the same question for every patient with gastric or gastroesophageal junction adenocarcinoma, for people outside the PD-L1-positive analysis set, or for treatment settings not represented in the trial record. The separate intention-to-treat secondary results address a broader analysis population, but they do not redefine the primary question.

A statistically notable result is not by itself a judgment about clinical importance, tolerability, or the balance of benefits and harms. The registry summary does not provide enough information to assess all those considerations or to make a treatment recommendation. The adverse-event counts are descriptive and do not establish individual causation. Decisions about care require clinical context that is outside this statistical analysis.

The result also does not prove that the hazard ratio is constant throughout follow-up. The registry record does not report an assessment of proportional hazards or present enough information to assess changes in relative effects over time. Nor does the primary analysis settle the results of every secondary endpoint, especially where p-values, multiplicity procedures, or numerical quality-of-life findings are not reported. The appropriate interpretation is therefore bounded: a reported comparative survival result for a defined population, endpoint, and cutoff, with remaining uncertainty and documentation limits.

19. Why This Trial Matters Statistically

This trial illustrates why the analysis population and endpoint need to be read together. The primary question is not simply whether one regimen was compared with another; it is whether overall survival differed in the PD-L1-positive analysis set under a specific time-to-event analysis. The registry record separately presents results for the intention-to-treat population and for progression-free survival, so each result needs to remain attached to its own population and outcome.

It also demonstrates the distinction between an arm-level summary and a comparative estimate. Median survival summarizes each group, while the hazard ratio compares event rates across follow-up. The confidence interval describes uncertainty around that comparative estimate. These summaries complement one another, but they are not interchangeable and should not be reduced to a single claim about every participant.

The study offers a useful example of how a primary endpoint can be accompanied by multiple secondary outcomes and analysis sets. That breadth can provide a fuller descriptive picture, but it also raises questions about multiplicity, prespecification, and missingness. Because those methods are not reported in the registry record, readers should distinguish the primary analysis from exploratory or less fully documented secondary evidence.

Finally, sample-size illustrations based on observed effects are different from the original design calculation and from observed power. Separating planning assumptions from the trial's actual reported analysis helps prevent retrospective calculations from being mistaken for evidence about design adequacy. This distinction is broadly important when interpreting registry results and summary-based calculations.

20. 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 primary analysis concerns the PD-L1-positive set rather than the full randomized population. The registry defines positivity by tumor PD-L1 TAP score, but the record does not provide a detailed account of biomarker availability or exclusions. The primary result therefore should not be generalized automatically beyond that defined set.

The primary survival analysis cutoff differs from the later cutoff used for the posted final-efficacy progression-free-survival results. The record gives the cutoffs and follow-up summaries, but does not explain the rationale for these analysis timings or provide a later overall-survival result. Comparisons across endpoints should account for their different observation periods.

The detailed statistical analysis plan is not reported in the registry record. In particular, the record does not describe covariate adjustment, proportional-hazards checks, missing-data procedures, interim analyses, multiplicity control, or the original sample-size justification. Those omissions limit assessment of the robustness and confirmatory status of the results; they do not establish that the study lacked these procedures.

The intervention descriptions are incomplete in the record. Although the named chemotherapy drugs and the general platinum-fluoropyrimidine approach are available, the full chemotherapy schedules are not present. Safety summaries also lack detailed information on event attribution, exposure, timing, and the causes of deaths. These limits mean the posted summary cannot support a complete comparison of treatment implementation or safety.

Finally, the interpretation is restricted to posted registry summaries. The record includes a sponsor-reported primary analysis, but does not include all participant-level data or the full analysis code. The secondary results are not all accompanied by p-values, and numerical results for some listed outcomes are absent. Conclusions should remain tied to the analyses and data actually reported.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Tislelizumab in Combination With Chemotherapy as First-Line Treatment in Adults With Inoperable, Locally Advanced or Metastatic Gastric, or Gastroesophageal Junction Carcinoma — NCT03777657.
• Registry record last updated 2025-02-14; status last verified 2025-01.
• Results first posted 2025-02-14.
• 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.

24. Record Summary

The registry record describes a completed randomized, double-blind, placebo-controlled, parallel-group phase 3 study sponsored by BeiGene, with triple masking recorded and enrollment of 997. It compared tislelizumab plus investigator-choice chemotherapy with placebo plus investigator-choice chemotherapy as first-line treatment for adults with locally advanced unresectable or metastatic gastric or gastroesophageal junction adenocarcinoma.

The primary endpoint was overall survival in participants whose tumors met the PD-L1-positive definition. The sponsor reported a hazard ratio of 0.74 with a 95% confidence interval from 0.59 to 0.94 and a one-sided log-rank p-value of 0.006 at the primary analysis cutoff of 8 October 2021. Secondary results cover other endpoints and analysis populations, but the registry record does not report several details needed to assess multiplicity, missing data, and the full analysis plan.