Docetaxel+Oxaliplatin+S-1 (DOS) Regimen as Neoadjuvant Chemotherapy in Advanced Gastric Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Docetaxel+Oxaliplatin+S-1 (DOS) Regimen as Neoadjuvant Chemotherapy in Advanced Gastric Cancer (NCT01515748), a randomized phase 3 study. The primary outcome is Percentage of Participants With 3-Year Progression-Free Survival (PFS), as Assessed by Response Evaluation Criteria in Solid Tumors (RECIST)1.1.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, open-label, parallel-group study in people with resectable advanced gastric cancer. The registry lists enrollment as 530 and status as completed. The study start date was 2011-12-30, and the primary completion date was 2019-01-21. The sponsor was Sanofi.

The two strategies shared surgery and adjuvant S-1. In the SC arm, participants underwent surgery within 2 weeks after randomization and then received adjuvant S-1. In the CSC arm, participants received neoadjuvant docetaxel, oxaliplatin and S-1, followed by surgery and adjuvant S-1. The record describes the trial as having no masking, so treatment assignment was open label.

The primary endpoint was the percentage of participants with 3-year progression-free survival. Its stated timeframe was 3 years, and the analysis used the Full Analysis Set definition described in the registry. For the CSC arm, that definition also specifies exposure to at least one dose of the investigational products. The registry record does not provide enough text to recover the complete arm-specific population definition.

The stated secondary objectives included overall survival, postoperative pathological stage, R0 resection and safety. The registry lists 10 outcome measures and reports 9 posted secondary outcomes. Original design assumptions, including the trial's sample-size justification and intended statistical analysis plan, are not reported in the registry record. Interim analyses and details of treatment allocation procedures beyond randomized allocation are also 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: Total of 530 participants were enrolled and randomized in study. Assignment was done using Interactive Web-Response System (IWRS) in 1:1 to treatment arms. Randomization was stratified by site and Tumor size, Lymph Nodes affected, Metastases (TNM) \[T2/N+,T3-4/N+,T4/N-\] stage.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS): included all randomized participants who satisfied inclusion/exclusion criteria and had at least one tumor assessment after baseline visit (Day 0). The CSC Arm included all participants exposed to at least one dose of Docetaxel+Oxaliplatin+S-1 investigational products. The SC Arm included all participants who had surgery.

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: Analysis was performed on Intent-to-Treat (ITT) population which included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With 3-Year Progression-Free Survival (PFS), as Assessed by Response Evaluation Criteria in Solid Tumors (RECIST)1.1, measured over 3 years.

The primary endpoint was the percentage of participants with 3-year progression-free survival, assessed by RECIST 1.1. Progression-free survival was defined as the time from randomization to objective tumor progression, recurrence or death. The reported endpoint therefore describes the proportion classified as progression-free at the stated 3-year time point; it is not simply a count of people whose tumors had not grown at a single clinic visit.

The registry's progression rules addressed events during treatment, surgery and follow-up. In the CSC arm, progression during neoadjuvant chemotherapy was determined according to RECIST 1.1. Distant metastasis found during surgery or reported from pathology, residual cancer at a resection margin that could not be completely removed, and residual cancer confirmed at the margin on postoperative histology were also treated as progression. After R0 resection, recurrence, distant metastasis or a new lesion was dated to the first tumor assessment when it was observed.

As a general statistical matter, a progression-free survival endpoint combines tumor progression and death into a clinically relevant time-to-event outcome. It can capture disease control over follow-up without requiring survival alone to be the only event of interest. Its interpretation depends on consistent event definitions, assessment timing and handling of participants without a recorded event. The registry record gives event definitions but does not report all details of follow-up completeness or missing-data handling.

7. Results Posted in the Registry

• Neoadjuvant Chemotherapy +Surgery +Adjuvant Chemotherapy (CSC): 67.0% (156/233) versus 60.2% (148/246) on control; risk difference 6.8 percentage points (95% CI -1.8 to 15.4), risk ratio 1.11 (0.97–1.27); unadjusted two-proportion z-test p = 0.123.

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 With R0 Resection

• 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:
  • Neoadjuvant Chemotherapy +Surgery +Adjuvant Chemotherapy (CSC): 95.5% (212/222) versus 83.7% (206/246) on control; risk difference 11.8 percentage points (95% CI 6.4 to 17.1), risk ratio 1.14 (1.07–1.21); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Neoadjuvant Chemotherapy +Surgery +Adjuvant Chemotherapy (CSC) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover overall survival, postoperative pathological stage response, R0 resection, treatment-emergent and serious adverse events, and laboratory changes. This is a broad set of efficacy and safety measures rather than a single secondary question. The posted results include an R0 resection comparison and safety information, but the registry record does not report secondary outcome results for every listed measure.

At a broad level, the posted R0 resection percentages are higher in the CSC arm than in the SC arm. This is consistent with a difference in a surgical outcome, but it is not interchangeable with the primary progression-free survival endpoint. Overall survival is a separate outcome, and its results are not reported in the registry record. Pathological response and laboratory changes likewise address different aspects of treatment and should not be treated as confirmation of the primary result.

Secondary findings can help describe the range of outcomes observed, but they generally carry less weight than a prespecified primary analysis when many outcomes are examined. As a general statistical matter, multiple comparisons increase the chance that at least one apparently notable result occurs by chance. The record does not report a multiplicity adjustment or a hierarchy governing interpretation of the secondary endpoints, so their p-values, where posted, should be considered unadjusted unless otherwise stated.

The secondary outcomes also differ in their denominators, timeframes and clinical meaning. Safety outcomes may depend on exposure and observation, while surgical outcomes are assessed among participants who reach surgery and have evaluable findings. Those distinctions make it important not to infer one global treatment effect from a collection of endpoint-specific results. Taken together, the secondary measures provide context for the primary comparison, but they do not resolve the limitations in the sponsor's primary result reporting or establish a single overall conclusion.

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

• Overall Survival (OS)
• Number of Participants With Post-Operative Pathological Stage Response
• Percentage of Participants With R0 Resection
• Number of Participants With Treatment Emergent Adverse Events (TEAEs) and Serious Adverse Events (SAEs)
• Number of Participants With Shift of Laboratory Parameters (Hematology) From Baseline Grade to Worst National Cancer Institute Common Terminology Criteria for Adverse Events (NCI-CTCAE) Grade >=3
• Number of Participants With Shift of Laboratory Parameters (Sodium and Potassium Levels) From Baseline Grade to Worst NCI-CTCAE Grade >=3
• Number of Participants With Shift of Laboratory Parameters (Calcium, Creatinine and Albumin Levels) From Baseline Grade to Worst NCI-CTCAE Grade >=3
• Number of Participants With Shift of Laboratory Parameters (Aspartate Aminotransferase, Alanine Aminotransferase,Blood Bilirubin,Alkaline Phosphatase and Glucose Levels) From Baseline Grade to Worst NCI-CTCAE Grade >=3

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the sponsor's primary analysis as a stratified log-rank test and classifies it as a superiority analysis. A separate simple re-calculation treats 3-year progression-free survival as a binary outcome and compares the posted counts in the two arms. These approaches answer related but not identical statistical questions. The registry record does not report the full analysis plan, stratification factors, or all details needed to reproduce the sponsor's calculation.

What does the log-rank method compare?

As a general statistical explanation, a log-rank test compares the pattern of event timing between groups across follow-up. Participants contribute information while they are observed and event-free; when an event occurs, it contributes to the comparison at that point in follow-up. Participants who have no recorded event before their observation ends are generally censored rather than counted as if an event occurred. This makes a time-to-event method different from comparing only the final status at a fixed time.

The primary endpoint was defined as time from randomization to progression, recurrence or death, and the registry reports a 3-year percentage as the primary outcome. The sponsor's stratified log-rank result uses the event-time framework. The registry does not state which variables defined the strata, how censoring was handled in detail, or whether assumptions and diagnostics were assessed. Those omissions mean the published test cannot be independently reconstructed from the record alone.

Why is the re-calculation different?

The re-calculated risk difference uses the posted counts and denominators as a binary comparison. Its estimate is 0.068, with a 95% confidence interval from -0.018 to 0.154 and an unadjusted p-value of 0.123. It does not use the timing of events, nor does it reproduce stratification. It is therefore a check based on the posted summary counts, not a replacement for the sponsor's analysis. The discrepancy flag indicates that the sponsor's own analysis takes precedence.

As a general matter, a risk difference expresses an absolute contrast between proportions. A confidence interval around it represents uncertainty in that contrast under the calculation's assumptions. When the interval includes zero, the data are compatible with no difference under that binary calculation, as well as with differences in either direction within the interval. That statement applies to the re-calculation, not automatically to the sponsor's time-to-event result.

What does stratification add?

In general, stratified analysis compares groups within categories defined before or during analysis, then combines information across those categories. This can account for specified factors in the comparison and can differ from an unstratified analysis. The registry names the method but does not report the stratification variables, so their role cannot be assessed from the record. No adjusted hazard ratio or its confidence interval is reported in the posted primary result.

How should the confidence intervals be read?

A confidence interval gives a range of estimates compatible with the data under a statistical procedure. It is not a guarantee that the true value falls inside that particular interval, and it is not a range of individual participant outcomes. The arm-specific intervals quantify uncertainty in each estimated 3-year percentage; the interval for the re-calculated risk difference quantifies uncertainty in that binary contrast. These intervals should not be substituted for an interval from the sponsor's time-to-event analysis, which is not reported in the registry record.

General statistical considerations also include missing assessments, loss to follow-up and event ascertainment. These can affect the number of participants with usable outcome information and the interpretation of censoring. Although the registry defines the Full Analysis Set as randomized participants who met eligibility criteria and had at least one post-baseline tumor assessment, it does not report the detailed missing-data methods, exclusions by reason, or sensitivity analyses. The group denominators in the posted estimates should therefore be read in the context of that stated population definition rather than assumed to represent every randomized participant.

The registry reports one primary analysis and lists secondary outcomes. It does not report whether the primary analysis was adjusted for other variables, whether there were planned interim looks, or how multiplicity was handled. These are elements of an analysis plan, not details that can be inferred from a method name. Without them, interpretation should remain tied to the stated endpoint, analysis population and reported test.

11. Confidence Intervals and Precision

The reported 3-year progression-free survival estimate for SC is 60.24%, with a 95% confidence interval from 53.55% to 66.28%. For CSC, the estimate is 66.82%, with a 95% confidence interval from 60.13% to 72.65%. The intervals express uncertainty around each arm's estimated percentage, not a range expected to contain most individual outcomes.

The unadjusted re-calculated risk difference has a 95% confidence interval from -0.018 to 0.154. Its span includes zero, so this summary-count comparison does not pin down the direction of the difference with high precision. It is compatible with a small contrast in either direction and with a larger positive contrast within its interval. The calculation is binary and unadjusted; it is not the sponsor's stratified log-rank analysis.

As a general concept, interval width reflects statistical precision: narrower intervals indicate estimates that are more tightly constrained under the method, while wider intervals leave greater uncertainty. Precision depends on factors such as the amount of outcome information and variability, but the registry does not report enough detail to attribute the observed widths to particular causes. The arm-specific intervals overlap, but overlap alone is not a formal test of the between-arm contrast.

The sponsor's reported primary analysis does not include an effect estimate or confidence interval in the registry record. Thus, the precision of the sponsor's time-to-event contrast cannot be assessed from the posted result. The registry gives a sponsor-reported stratified log-rank test and a separate binary re-calculation; these should not be merged into a single estimate.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for this binary outcome, not total events. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. It uses the observed effect as a reference and considers detecting the stated fraction of that effect. These are planning illustrations, not observed power.

For 100% of the observed effect, the illustration gives 788 participants per arm for 80% power and 1,054 participants per arm for 90% power. For 75% of the observed effect, it gives 1,415 participants per arm for 80% power and 1,893 participants per arm for 90% power. For 50% of the observed effect, it gives 3,212 participants per arm for 80% power and 4,300 participants per arm for 90% power.

In plain language, the 80% power column describes a planning target under which a study of the indicated size would have an 80% chance of detecting the specified effect if that effect were real and the assumptions held. The 90% power column uses a higher chance of detection and therefore calls for more participants under the same assumptions. The figures are not a retrospective statement about whether this trial had adequate power.

The pattern reflects a general design principle: smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of an observed effect requires more participants. These calculations use the observed effect as their reference and are not the trial's original design justification. The original sample-size assumptions and justification are not reported in the registry record.

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 = 0.602; treatment proportion p₁ = 0.670; average p̄ = 0.636.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6806 = 1.3340.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6789 = 0.5714.
4. n = (1.3340 + 0.5714)² / (0.0679)² = 787.4, rounded up to 788 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 <- 0.601626016260163                          # control proportion
p1 <- 0.669527896995708                          # 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(1515748)
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 = 788 (80% power), 1,054 (90% power)
 75% of observed effect: n per arm = 1,415 (80% power), 1,893 (90% power)
 50% of observed effect: n per arm = 3,212 (80% power), 4,300 (90% power)
power.prop.test: 787.4 
Simulated power at n = 788 per arm: 0.800 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor's primary analysis is reported as a stratified log-rank test and categorized as a superiority analysis. Its exact p-value is reported in the registry record, but no sponsor effect estimate or confidence interval accompanies that result. The registry also flags a discrepancy between the sponsor analysis and the simple re-calculation.

The re-calculation uses the posted event counts and denominators to compare the 3-year outcome as a binary proportion. It gives an unadjusted risk difference of 0.068, a 95% confidence interval from -0.018 to 0.154 and an unadjusted p-value of 0.123. It does not account for event timing or reproduce the stratified log-rank method. It is therefore a separate, limited check rather than an alternative version of the sponsor's primary analysis.

Because the discrepancy is flagged, the sponsor's own analysis takes precedence. The registry's reported superiority classification belongs to the sponsor's time-to-event test; it should not be reassigned to the binary re-calculation. At the same time, the missing sponsor effect estimate, confidence interval and details of stratification make the magnitude and precision of that analysis difficult to evaluate independently. The registry record does not report enough methodological detail to resolve the difference by reproducing the sponsor's test.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and 9 posted secondary outcomes. It does not report whether statistical testing across these outcomes was adjusted for multiplicity, whether an ordered testing strategy was used, or whether any outcomes were considered exploratory. Those details are not reported in the registry record. Without them, secondary results should not be interpreted as if each had been protected by a prespecified family-wise error strategy.

The sponsor's primary test is identified as a stratified log-rank analysis, but the record does not provide a full statistical analysis plan, the stratification factors, or the primary effect estimate and confidence interval. The reported result is classified as a superiority analysis. Interim analyses and any associated stopping rules are not reported in the registry record, nor is the original sample-size justification.

The stated Full Analysis Set included randomized participants who satisfied inclusion and exclusion criteria and had at least one tumor assessment after baseline. The record further says the CSC arm included participants exposed to at least one dose of the investigational products, but the remaining text of the population description is incomplete. The extent to which participants were excluded from the endpoint analysis, and the reasons for any exclusions, are not reported in the registry record.

Detailed missing-data methods are not reported. In particular, the record does not state how missing tumor assessments, loss to follow-up, or participants without a documented event were handled, or whether sensitivity analyses were performed. For a time-to-event endpoint, censoring assumptions and follow-up completeness matter because participants with no recorded event contribute information only up to the time they are observed. The posted endpoint estimates should therefore be interpreted within the limits of the population and methods that are explicitly described.

These omissions do not show that the analyses were inappropriate; they limit what can be checked from the registry record. They also make it difficult to determine how selective reporting, multiple testing or missing outcomes may have affected the interpretation of the secondary findings.

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: febrile neutropenia (8.7%), abdominal pain (5.0%), enteritis (3.1%), ileus (3.1%), diarrhoea (2.1%).

The registry lists serious adverse events among 57 of 195 participants at risk in the SC group and 102 of 241 participants at risk in the CSC group. These are counts and denominators reported for the serious adverse event summary. They should be read as the posted group-level figures, not as a causal comparison or as a complete description of event severity, duration or attribution.

The listed serious adverse event terms include febrile neutropenia at 8.7%, abdominal pain at 5.0%, enteritis at 3.1%, ileus at 3.1%, diarrhoea at 2.1% and mechanical ileus at 2.1%. These are reported terms and percentages; the registry record does not provide all details needed to interpret their timing, overlap within participants, or relationship to treatment. Participants can experience more than one event, so term-level figures should not be added together.

As a general statistical matter, safety comparisons depend on exposure, time at risk, event ascertainment and how events are defined. The registry provides serious adverse event figures but does not report enough detail to adjust for those factors. They describe reported events in the trial groups and do not alone establish whether one strategy is safer.

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

The posted results show 3-year progression-free survival estimates of 60.24% in the surgery plus adjuvant S-1 group and 66.82% in the neoadjuvant chemotherapy plus surgery and adjuvant S-1 group. The registry also reports a sponsor-conducted stratified log-rank superiority analysis. Its result is distinct from a simple binary re-calculation of the endpoint, which produces an unadjusted risk difference with a confidence interval that includes zero. The registry flags this discrepancy, so the sponsor's own analysis takes precedence.

The data do not show that every participant in one group had a better outcome than every participant in the other. Group-level estimates describe averages or proportions, not individual outcomes. Nor do the posted results isolate the effect of any single drug: the trial compared two treatment strategies that shared surgery and adjuvant S-1 but differed in the addition of neoadjuvant docetaxel, oxaliplatin and S-1.

The registry record does not provide the sponsor's primary effect estimate and confidence interval, the full statistical analysis plan, or sufficient detail to reproduce the stratified test. The posted primary percentages and their confidence intervals describe the arms, but they do not substitute for a contrast estimate from the sponsor's time-to-event analysis. The binary re-calculation is also not a substitute for that analysis because it does not use event timing.

Secondary outcomes, including overall survival, pathological response, resection status and safety, address different questions. Some secondary results are posted, but the registry record does not report results for every listed outcome or a multiplicity plan. Those measures may provide context but should not be treated as a single confirmatory body of evidence.

These findings describe the trial and the analyses recorded in the registry. They do not establish that a treatment works or does not work for an individual, and they should not be treated as medical advice. Interpretation beyond the trial requires attention to the study population, treatment delivery, follow-up, event definitions and the limitations of the available statistical reporting.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two treatment strategies using a time-to-event primary endpoint, while the registry also makes a fixed-time percentage available. The distinction matters: an analysis of event timing can use follow-up information differently from a binary comparison at 3 years. Treating those methods as interchangeable would obscure the reason their results can differ.

The record explicitly flags a discrepancy between the sponsor's stratified log-rank analysis and the simple unadjusted re-calculation. That makes transparent reporting of the primary effect estimate, confidence interval, analysis population, stratification factors and missing-data approach especially important. The registry reports the sponsor's superiority classification and test method, but does not supply enough analytical detail to reproduce the result or assess its precision directly.

The trial also illustrates why a nominal primary outcome and a broad collection of secondary outcomes need distinct interpretive roles. Overall survival, surgical findings and safety measures may address important questions, but multiple outcomes create opportunities for chance findings unless an analysis hierarchy or multiplicity approach is specified. That approach is not reported in the registry record.

Finally, the planning illustrations show how assumptions about the effect to be detected influence sample-size requirements. They are not evidence of the trial's observed power and are not a substitute for its original design justification, which is not reported. Together, these features make the trial a useful example of how endpoint definition, analysis method, precision and reporting completeness shape interpretation of clinical trial results.

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.

Several limitations specific to this trial affect interpretation of the posted results. The sponsor's primary result is identified as a stratified log-rank superiority analysis, but the registry does not report its effect estimate or confidence interval. The registry also does not identify the stratification factors or provide enough information to reproduce the test. The discrepancy flag further distinguishes this result from the unadjusted binary re-calculation.

The primary endpoint population definition is incomplete in the registry text. The available description says the Full Analysis Set included randomized participants who met eligibility criteria and had at least one post-baseline tumor assessment, and gives an additional exposure condition for the CSC arm. The remainder of the definition is truncated. The record does not report the number or reasons for exclusions from the primary analysis.

Missing-data handling, censoring details, follow-up completeness and sensitivity analyses are not reported in the registry record. These details are relevant to a progression-free survival analysis because event status and observation time determine how participants contribute information. The registry also does not report the trial's original sample-size justification, interim analyses or full statistical analysis plan.

The record lists multiple secondary outcomes but does not report results for all of them or explain whether multiplicity was controlled. Safety summaries are available, but details such as event timing, overlap, exposure duration and attribution are not fully described in the posted information. These limitations restrict the strength and scope of conclusions that can be drawn from the registry record; they do not by themselves establish that the underlying trial methods were inadequate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Docetaxel+Oxaliplatin+S-1 (DOS) Regimen as Neoadjuvant Chemotherapy in Advanced Gastric Cancer — NCT01515748.
• Registry record last updated 2023-12-13; status last verified 2023-11.
• Results first posted 2020-03-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT01515748 is a completed, randomized, open-label, parallel-group phase 3 trial sponsored by Sanofi in resectable advanced gastric cancer. It compared neoadjuvant docetaxel, oxaliplatin and S-1 followed by surgery and adjuvant S-1 with surgery followed by adjuvant S-1. The primary outcome was 3-year progression-free survival.

The registry reports arm-level primary estimates and a sponsor-reported stratified log-rank superiority analysis. A separate unadjusted binary re-calculation differs, and the discrepancy is flagged; the sponsor's analysis takes precedence. The record also lists secondary efficacy and safety outcomes, but the full statistical plan, key analysis details, and results for every secondary outcome are not reported in the registry record.