Combination Chemotherapy With or Without Vismodegib in Treating Patients With Advanced Stomach Cancer or Gastroesophageal Junction Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Combination Chemotherapy With or Without Vismodegib in Treating Patients With Advanced Stomach Cancer or Gastroesophageal Junction Cancer (NCT00982592), a randomized phase 2 study. The primary outcome is Median Progression-free Survival (PFS).

2. Clinical Question

The trial addresses whether adding vismodegib to FOLFOX changed progression-free survival compared with FOLFOX plus placebo. It was randomized, double blind, and parallel group, which means participants were assigned to one of two groups and followed under the assigned regimen. The registry lists an enrollment of 124.

The clinical question is about the comparative outcome of the treatment regimens in this trial, not about FOLFOX in isolation. Because both groups received FOLFOX, the comparison concerns the addition of vismodegib rather than chemotherapy versus no chemotherapy. The registry's brief description states that it was not known whether FOLFOX was more effective with or without vismodegib. The results should therefore be read as a comparison of the two assigned regimens in this study population, rather than as a general claim about all patients with these cancers or all uses of these drugs.

3. Trial Design

This was a randomized, double-blind, parallel-group phase 2 study sponsored by the National Cancer Institute. The registry reports an enrollment of 124 and identifies two groups: FOLFOX plus placebo and FOLFOX plus vismodegib. The primary outcome population was intent-to-treat. The registry record does not report the allocation ratio, randomization sequence method, concealment procedure, or the details of how double blinding was maintained.

FOLFOX consisted of oxaliplatin, leucovorin calcium, and fluorouracil. In the placebo group, the registry describes intravenous chemotherapy on day 1 and placebo by mouth on days 1–14. The vismodegib group received the same FOLFOX regimen and vismodegib by mouth on days 1–14. Courses were to repeat every 2 weeks unless unacceptable toxicity or disease progression occurred. The description of the placebo-arm course is truncated in the registry record, so no additional stopping conditions can be inferred for that description.

The study start is listed as 2009-09, primary completion as 2012-04, and status as completed. The primary outcome was median progression-free survival, with a timeframe of up to 4 years. The secondary outcomes listed include objective response rate, overall survival, and toxicities by grade. The registry record does not report the original sample-size justification, planned recruitment target beyond the enrollment listing, stratification factors, interim monitoring plan, or detailed statistical analysis plan. Those design details should not be reconstructed from the posted outcome estimates.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat population

5. Baseline Characteristics

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

Population: all the patients enrolled to the study

6. Primary Endpoint

The registry lists the primary outcome as Median Progression-free Survival (PFS), measured over up to 4 years.

Progression-free survival (PFS) measures the time from randomization until objective tumor progression or death from any cause. The registry states that progression was evaluated using Response Evaluation Criteria in Solid Tumors (RECIST) 1.1. The primary result is reported as median PFS in months with a 95% confidence interval, for the intent-to-treat population, over a timeframe of up to 4 years.

A time-to-event endpoint uses both the timing of an event and whether the event has occurred during follow-up. The median is the point in the estimated outcome distribution at which half of the population has experienced the event; it is not an average survival time. Participants whose event time is not observed within follow-up may contribute information up to their last known event-free assessment, a general feature of time-to-event analyses. The registry record does not report the specific censoring rules or follow-up completeness for this trial.

PFS is used in oncology trials because it captures progression as well as death, rather than requiring death to occur before an outcome is counted. It can therefore describe disease control over the observation period while retaining a time dimension. PFS does not, by itself, establish how participants felt or functioned, nor does it replace overall survival or safety outcomes. Interpretation depends on the endpoint definition, assessment schedule, follow-up, and analysis method. Details of assessment timing and the handling of missing evaluations are not reported in the registry record.

7. Results Posted in the Registry

• Arm I (FOLFOX Regimen and Placebo) vs Arm II (FOLFOX Regimen and Vismodegib): hazard ratio 1.03 (95% CI 0.70–1.54), reported p = 0.874 (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.

Objective Response Rate

• 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:
  • Arm II (FOLFOX Regimen and Vismodegib): 36.7% (22/60) versus 43.8% (28/64) on control; risk difference -7.1 percentage points (95% CI -24.3 to 10.1), risk ratio 0.84 (0.54–1.29); unadjusted two-proportion z-test p = 0.422.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (FOLFOX Regimen and Vismodegib) and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival

• 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:
  • Arm I (FOLFOX Regimen and Placebo) vs Arm II (FOLFOX Regimen and Vismodegib): hazard ratio 1.30 (95% CI 0.83–2.05), reported p = 0.253 (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 Arm I (FOLFOX Regimen and Placebo) vs Arm II (FOLFOX Regimen and Vismodegib) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide supporting context across response, survival, and toxicity rather than a single additional test of the primary question. Across these outcomes, the posted pattern does not supply a consistent, precise signal that changes the interpretation of the primary PFS comparison. The secondary results should be considered alongside the primary endpoint, the width of their uncertainty intervals where reported, and the fact that several outcomes were assessed.

Objective response describes whether a participant met the response definition during the specified period; overall survival is another time-to-event outcome, but it counts death rather than progression or death. These outcomes answer related but different questions. A response result cannot establish a difference in PFS, and a difference in median overall survival would not by itself show how progression was affected. The registry lists toxicity outcomes by grade as well, which concern harms and do not function as efficacy tests.

Unadjusted secondary results carry less weight when multiple outcomes are examined because the chance of at least one apparently unusual result can increase across a collection of tests. This is a general multiplicity concern. The registry record does not report a multiplicity adjustment, a hierarchy for secondary outcomes, or a confirmatory role for these analyses. Objective response also has no sponsor-reported comparative analysis listed. Accordingly, secondary findings are best treated as descriptive or supportive unless a prespecified analysis plan establishes otherwise; such a plan is not reported in the registry record.

The secondary outcomes do not erase the primary result, and they should not be combined informally into a single claim. Interpretation should preserve the distinctions between a binary response endpoint, a time-to-event endpoint, and safety summaries. The posted results offer additional observations about the trial, but the available record does not establish that every secondary analysis was designed or powered to make a definitive comparative conclusion.

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

• Objective Response Rate
• Overall Survival
• Incidence of Toxicities (Grade 3 and Higher)
• Incidence of Toxicities (grades1 and 2)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is time-to-event data. For each participant, the relevant outcome is the time from randomization to progression or death, as defined in the registry. Time-to-event methods are useful when participants have different follow-up times or when some do not experience the event during observed follow-up. General statistical practice is to retain information from such participants up to their last known event-free time, using censoring; the registry record does not specify the censoring rules used in this analysis.

What does a median describe?

The median PFS is a summary of the estimated event-time distribution. It marks the time at which the estimated proportion remaining progression-free reaches one half. It is not the arithmetic average of individual follow-up times, and it does not say that every participant in a group had an outcome close to that value. The posted medians are 8.77 months for FOLFOX plus placebo and 8.35 months for FOLFOX plus vismodegib. Their confidence intervals describe uncertainty in each group-level median estimate; they are not ranges containing a stated proportion of individual participants' PFS times.

How should the hazard ratio be read?

The registry reports a log-rank analysis and hazard ratio for the primary comparison. 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. The reported comparison is placebo versus vismodegib: HR 1.03, 95% CI 0.70 to 1.54, p = 0.874. A hazard ratio is not a ratio of median times and should not be read as a percentage change in median PFS. Its usual single-number interpretation is most straightforward when the relative hazards are reasonably stable over time; whether that assumption was checked is not reported in the registry record.

The log-rank test is a general method for comparing time-to-event experience between groups. It uses event timing across follow-up rather than comparing only the two median estimates. The p-value describes how compatible the observed test statistic is with a null hypothesis of no group difference under the test's assumptions. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. The registry reports p = 0.874 for the primary comparison but does not report a pre-specified decision threshold for that analysis.

What does the confidence interval contribute?

A confidence interval communicates the precision of an estimate under the model and sampling assumptions used. The primary HR interval, 0.70 to 1.54, includes the value 1, which corresponds to no relative difference in hazards. It also spans values on both sides of 1, so the data are compatible with more than one direction of relative effect. The interval is therefore important alongside the point estimate and p-value. The reported interval does not prove that all values inside it are equally plausible, and it does not account for every possible source of bias or uncertainty.

For the group-specific medians, the intervals are 5.65 to 10.61 months for placebo and 5.55 to 10.61 months for vismodegib. Comparing overlap between two separate confidence intervals is not the same as testing the treatment contrast. The sponsor's reported hazard-ratio analysis is the direct comparative time-to-event result in the registry record and should be used for the primary group comparison.

Why can over-dispersion matter?

Over-dispersion is a general statistical issue in count or binary data when observed variability exceeds what a simple model assumes. If it is present and not accommodated, standard errors can be too small and confidence intervals or tests can be misleading. The posted primary endpoint is time-to-event, and the registry record does not report an over-dispersion assessment or an analysis of this kind. The concept is included as general statistical context, not as a claim about this trial's data or analysis.

The registry identifies an intent-to-treat population for the primary endpoint, which generally means participants are analysed according to their randomized group. This preserves the randomized comparison as a central basis for interpretation. The record does not report the exact handling of participants with missing assessments, protocol deviations, or other analysis details. It also does not report checks of proportional hazards, sensitivity analyses, or any alternative time-to-event model. Such details should not be assumed based on the reported HR alone.

11. Confidence Intervals and Precision

The primary PFS medians are 8.77 months, with a 95% confidence interval of 5.65 to 10.61 months, for FOLFOX plus placebo, and 8.35 months, with a 95% confidence interval of 5.55 to 10.61 months, for FOLFOX plus vismodegib. These intervals reflect uncertainty in the median estimates. Their overlap indicates that each group median is estimated with a range of uncertainty that shares values with the other group's range, but overlap is not itself a formal test of the treatment difference.

The direct comparative estimate is the sponsor-reported hazard ratio of 1.03, with a 95% confidence interval of 0.70 to 1.54. The interval includes the null value of 1 and extends in both directions around it. This means the result is not precise enough to distinguish a range of possible relative event rates from no difference using the reported estimate alone. The p-value, 0.874, is consistent with the absence of strong evidence against the no-difference null in the log-rank comparison. Neither the p-value nor the interval establishes that the groups are equivalent.

Confidence intervals describe sampling uncertainty under the analysis assumptions; they do not automatically capture problems such as incomplete follow-up, measurement error, or bias. The registry record does not report enough detail on missing data, censoring, or model checks to assess those sources further. The enrollment was 124, but the number at risk for the primary time-to-event analysis at each follow-up time is not reported. The interval should therefore be read as a measure of statistical precision for the reported model, not as a complete account of uncertainty in every aspect of the trial.

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 the observed effect, not the trial's original design calculations. For objective response, values are participants per arm. For time-to-event outcomes, values are total events across groups. The distinction matters: a participant count per arm is not directly interchangeable with an event total, because the event total depends on how many participants experience the event during follow-up.

The assumptions used for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. For time-to-event outcomes, the event calculations use the Schoenfeld method. The original trial's own sample-size justification and design assumptions are not reported in the registry record.

The 80% power column represents the planning number that would give an 80% chance of detecting the specified effect if that effect were true and the planning assumptions held. The 90% power column targets a higher chance of detection, and therefore generally requires more information. For objective response, planning for 100% of the observed effect gives 751 participants per arm for 80% power and 1,005 participants per arm for 90% power. For primary PFS at the same effect fraction, the corresponding planning figures are 35,934 total events for 80% power and 48,105 total events for 90% power.

When planning for 75% or 50% of the observed effect, the target effect is smaller, and the required sample size or event total increases. These are prospective planning illustrations, not observed power; observed power is not a useful substitute for interpreting the confidence interval and estimate after results are known. The large extrapolated requirements should be read in relation to the observed effect used for the calculation, not as a report of the trial's actual enrollment 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 = 1.030, so ln(HR) = 0.0296.
2. d = 4 × (1.96 + 0.842)² / [ln(1.030)]² = 35,933.0, rounded up to 35,934 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 <- 1.03                              # 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(982592)
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 = 35,934 (80% power), 48,105 (90% power)
 75% of observed effect: events = 63,881 (80% power), 85,519 (90% power)
 50% of observed effect: events = 143,733 (80% power), 192,417 (90% power)
Simulated power with 35,934 events: 0.801 (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. Analyses Reported by the Sponsor

The registry reports a sponsor analysis for the primary PFS comparison using a log-rank method: HR 1.03, 95% CI 0.70 to 1.54, p = 0.874. The posted primary medians and their intervals are also given by group. The record does not flag a discrepancy between the sponsor's result and the calculations represented in the posted data. For the primary time-to-event comparison, the sponsor-reported hazard ratio is the analysis to emphasize.

A recalculation from posted summary statistics is a simple, unadjusted check and may not reproduce the full analysis. A time-to-event analysis can use participant-level event times, censoring information, and analysis choices that cannot be reconstructed from medians alone. The registry record does not include the participant-level data or the full analysis specification. Therefore, a summary-based calculation should not be treated as a replacement for the sponsor's log-rank result.

The objective-response comparison has no sponsor-reported comparative analysis listed. Any unadjusted contrast derived from the posted counts is descriptive and should be distinguished from the sponsor-reported PFS and overall-survival analyses. The registry record does not report whether a separate adjusted model was used for objective response.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes: primary PFS, objective response, overall survival, and toxicity outcomes by grade. When many endpoints or comparisons are examined, the chance of finding at least one apparently notable result by chance can increase. A multiplicity strategy may address this through adjusted tests, a prespecified hierarchy, or clearly designated exploratory analyses. Whether any such strategy was used is not reported in the registry record. The posted results should therefore not be read as though every endpoint had the status of a single prespecified primary test.

The primary analysis population is identified as intent-to-treat. That designation helps clarify that the primary comparison concerns randomized groups, but it does not specify how missing measurements, withdrawals, treatment changes, or protocol deviations were handled. The registry record does not report the number of participants with missing PFS assessments, the censoring rules, sensitivity analyses for missing data, or the analysis populations used for each secondary outcome. The number randomized and the number contributing to each specific analysis may consequently differ, but the details are not reported in the registry record.

For time-to-event outcomes, incomplete observation is commonly handled by censoring, but the assumptions and implementation matter. The registry does not describe censoring patterns, follow-up completeness, or whether loss to follow-up differed between groups. It also does not report whether the proportional-hazards assumption was checked for the hazard-ratio analyses. These omissions limit assessment of robustness; they do not establish that the analysis was inappropriate.

The registry provides the outcome definitions and selected estimates, but not a complete statistical analysis plan. Details about interim analyses, stopping rules, covariate adjustment, subgroup analyses, and sensitivity analyses are not reported in the registry record. Without those details, the safest interpretation is to give greatest emphasis to the named primary endpoint and to treat the remaining outcomes as secondary evidence whose role and multiplicity handling are unclear.

16. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: dyspnea (shortness of breath) (7.9%), thrombosis/thrombus/embolism (7.9%), neutrophils/granulocytes (anc/agc) (7.7%), death not associated with ctcae term: disease progression nos (5.8%), dehydration (5.8%).

The registry lists serious adverse events for 63 participants at risk in the FOLFOX-plus-placebo group, with 24 affected, and for 52 participants at risk in the FOLFOX-plus-vismodegib group, with 20 affected. These are the registry's serious-event counts and denominators; they are not the randomized group sizes used for the primary endpoint. The record also lists other adverse events for all participants at risk in each safety group, but does not provide a detailed interpretation of the event definitions in the summary presented.

The listed serious-event terms include dyspnea, thrombosis/thrombus/embolism, neutrophils/granulocytes, disease progression not associated with a CTCAE term, dehydration, and fatigue. The registry gives frequencies for these terms but does not identify a comparative statistical analysis for them in the posted record. The terms should not be treated as proof of a causal relationship to a particular regimen. A serious adverse event is a safety-reporting category, and counts can include participants with more than one event; the record does not specify how repeated events were handled in the summary.

Deaths are not reported as a separate count in the safety summary. The safety figures describe what was recorded, but do not by themselves establish comparative safety, event severity patterns beyond the listed categories, or the cause of individual events.

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

The result means that the registry's primary analysis did not show a clear PFS difference between the two randomized regimens. The median estimates are similar, and the sponsor-reported hazard ratio is close to 1 with a confidence interval that includes 1. This combination of findings indicates uncertainty around the size and direction of any comparative effect, rather than proof that there is no effect.

The result does not demonstrate equivalence, non-inferiority, or that the regimens have identical outcomes. Those conclusions require a suitable design and prespecified margins or hypotheses, which are not reported in the registry record. Nor does a non-significant p-value mean there is a specified probability that the treatments are the same. It describes the compatibility of the observed test result with a null hypothesis under the analysis assumptions.

The trial compares FOLFOX plus vismodegib with FOLFOX plus placebo in the enrolled study population. It does not compare FOLFOX with no chemotherapy, and it does not establish outcomes for populations or care settings not represented in the trial. The secondary results provide additional information but do not change the limits of the primary comparison; their analysis role and multiplicity handling are not reported in the registry record.

These findings are statistical descriptions of the posted trial results and should not be used as individual medical advice. The registry record does not provide full details on missing data, follow-up, treatment adherence, or the original design assumptions. Those limitations mean the estimates should be interpreted with attention to both the observed data and the uncertainty around them, rather than as a final answer about every possible use of either regimen.

18. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through its endpoint definition, effect estimate, and precision together. The reported medians offer an accessible summary of PFS in each group, while the hazard ratio and log-rank test provide the comparative time-to-event analysis. The HR confidence interval is essential: the point estimate alone would conceal the breadth of values compatible with the posted result.

It also demonstrates the difference between failing to find a statistically clear difference and proving that two regimens are equivalent. The primary estimate is near the null, but its interval still includes effects in either direction. The design's phase 2 label and enrollment of 124 provide context for the study, but do not by themselves establish whether the trial was adequately sized for a particular effect. The original sample-size justification is not reported in the registry record.

The planning illustrations underscore another general lesson: sample-size calculations depend on an effect target and assumptions. They are not observed power and should not be confused with the enrollment actually achieved. For time-to-event calculations, the target is expressed in total events; for the binary response endpoint, it is expressed as participants per arm. Those quantities reflect different analysis structures.

Finally, the record highlights the importance of transparency about multiplicity, missing data, censoring, and analysis populations. Those details shape how confidently estimates can be interpreted, especially when there are multiple secondary outcomes. The posted findings are informative, but their limits are part of the statistical result, not an afterthought.

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.

The registry record gives selected outcome estimates but not a complete statistical analysis plan. The original sample-size rationale, allocation ratio, randomization details, and any stratification factors are not reported in the registry record. As a result, the intended detectable effect and the design's assumptions cannot be assessed from the posted results.

For PFS and overall survival, the record reports medians and hazard ratios but does not describe censoring rules, follow-up completeness, the number at risk over time, or checks of the proportional-hazards assumption. It also does not report how missing assessments or protocol deviations were handled. These details are important for evaluating time-to-event estimates and their robustness.

The record lists multiple secondary outcomes but does not report a multiplicity strategy or a hierarchy among them. A sponsor-reported comparative analysis is listed for PFS and overall survival, while none is listed for objective response. The record also does not give comparative statistical analyses for the reported toxicity categories. Thus, the relative confirmatory status and interpretation of the secondary findings are not fully clear.

The study is a phase 2 trial with enrollment of 124, so estimates may remain imprecise, as reflected in the primary HR interval. The registry record does not report enough information to determine whether the study was intended to support a definitive confirmatory conclusion. The arm description for FOLFOX plus placebo is truncated, and the detailed trial protocol, adherence, treatment exposure, and complete safety follow-up are not reported in the registry record. These gaps limit interpretation of implementation and generalizability without invalidating the outcomes that are posted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Combination Chemotherapy With or Without Vismodegib in Treating Patients With Advanced Stomach Cancer or Gastroesophageal Junction Cancer — NCT00982592.
• Registry record last updated 2016-01-25; status last verified 2015-08.
• Results first posted 2016-01-25.
• 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

NCT00982592 is a completed randomized, double-blind, parallel-group phase 2 trial sponsored by the National Cancer Institute. It enrolled 124 participants with advanced gastric or gastroesophageal junction cancer and compared FOLFOX plus placebo with FOLFOX plus vismodegib. The study began in 2009-09, and primary completion is listed as 2012-04.

The primary endpoint was median PFS in the intent-to-treat population, defined as time from randomization to objective progression or death. The sponsor-reported comparison was HR 1.03, 95% CI 0.70 to 1.54, p = 0.874. The posted results do not establish equivalence, and the confidence interval reflects uncertainty about the comparative effect. Secondary outcomes include objective response, overall survival, and toxicities. Details of the original sample-size justification, multiplicity handling, and missing-data methods are not reported in the registry record.