Gemcitabine Hydrochloride With or Without Vismodegib in Treating Patients With Recurrent or Metastatic Pancreatic Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Gemcitabine Hydrochloride With or Without Vismodegib in Treating Patients With Recurrent or Metastatic Pancreatic Cancer (NCT01064622), a randomized phase 2 study. The primary outcome is Progression-free Survival.

2. Clinical Question

The clinical question was whether adding vismodegib to gemcitabine changed the time until progression or death compared with gemcitabine alone. The trial was randomized, double-blind, and placebo-controlled, which supports a comparison between assigned treatment groups while limiting some sources of bias. The registry identifies the study as a phase II trial and reports enrollment of 118 participants.

The primary endpoint was progression-free survival, with overall survival and objective response rate among the secondary outcomes. These outcomes address different aspects of the trial: progression-free survival tracks time to progression or death, overall survival tracks time to death, and response rate records whether a specified tumor response occurred. The registry also lists adverse events and activity among crossover patients as secondary outcomes. Numerical crossover response results are not reported in the registry record.

3. Trial Design

The registry describes a randomized, double-blind, parallel-group phase II trial sponsored by the National Cancer Institute. Its listed enrollment was 118. The trial compared gemcitabine hydrochloride plus placebo with gemcitabine hydrochloride plus vismodegib. The registry records the study as completed, with a start date of 2009-09-03 and primary completion on 2012-12-09.

In both arms, gemcitabine was administered intravenously over 30 minutes on days 1, 8, and 15. The placebo or vismodegib was taken orally each day on days 1–28. Courses were scheduled to repeat every 28 days in the absence of progression or unacceptable toxicity. The registry describes placebo as the masked comparator, consistent with the double-blind design.

At disease progression, patients in the gemcitabine-and-placebo arm were to be unblinded and could cross over to the vismodegib arm. That option matters when interpreting outcomes after progression: the randomized comparison concerns initial assignment, while later treatment could differ for crossover patients. The registry lists 53 participants in each randomized group for the posted efficacy outcomes. It also identifies phase I lead-in patients, but says they were not included in the efficacy analysis.

The primary endpoint was assessed for up to 3 years. The registry describes estimation by the Kaplan–Meier method and comparison by a stratified log-rank test. It does not report the original design assumptions, the stratification factors, or details of the randomization procedure beyond randomized allocation. Information about interim analyses is 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: Prior to the phase II randomized trial, an open-label, lead-in phase I study was conducted with all patients receiving gemcitabine hydrochloride plus vismodegib. Seven patients were enrolled and no safety issues were identified.

Lead-in Phase I

Randomized Phase II

Reasons for not completing this period:

Crossover of Arm I

Analysis population for the primary outcome, as defined in the registry: Phase I lead-in patients were not included in the efficacy analysis.

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 Progression-free Survival, measured over Up to 3 years.

Progression-free survival was defined as the time from randomization to disease progression or death from any cause. This endpoint combines two clinically relevant events into a time-to-event measure. It can describe how long participants remain alive without recorded progression, rather than only whether progression has occurred at a particular visit.

The registry reports median progression-free survival for each treatment group and a hazard ratio from the group comparison. The median is the estimated time by which half of the analyzed group has experienced the event, under the time-to-event analysis. A hazard ratio compares the event rates over follow-up as represented by the model; its interpretation depends on the order and coding of the groups. The registry identifies the sponsor’s method as a stratified log-rank test and the estimation method as Kaplan–Meier.

In general, time-to-event methods are useful when participants can have different follow-up durations or when the event has not occurred for everyone by the end of observation. They use information about both the timing of events and the time participants remain under observation. The registry states a timeframe of up to 3 years, but specific follow-up distributions and handling of incomplete observations are not reported in the registry record.

The endpoint should be read as a measure of time to progression or death in the trial’s analyzed population. It is not a direct measure of tumor response alone, and it does not by itself describe overall survival or adverse effects. Those are distinct outcomes, with separate results in the record.

7. Results Posted in the Registry

• Arm I (Gemcitabine Hydrochloride and Placebo) vs Arm II (Gemcitabine Hydrochloride and Vismodegib): hazard ratio 0.82 (95% CI 0.55–1.22), reported p = 0.150 (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.

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 (Gemcitabine Hydrochloride and Placebo) vs Arm II (Gemcitabine Hydrochloride and Vismodegib): hazard ratio 0.96 (95% CI 0.64–1.46), reported p = 0.370 (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 (Gemcitabine Hydrochloride and Placebo) vs Arm II (Gemcitabine Hydrochloride and Vismodegib) and the control. The interval gives the range of effects that remain compatible with the data.

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 (Gemcitabine Hydrochloride and Vismodegib): 7.5% (4/53) versus 13.2% (7/53) on control; risk difference -5.7 percentage points (95% CI -17.2 to 5.9), risk ratio 0.57 (0.18–1.84); unadjusted two-proportion z-test p = 0.339.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Gemcitabine Hydrochloride and Vismodegib) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context by addressing survival, tumor response, safety, and activity among crossover patients. Overall survival is a distinct time-to-event outcome from progression-free survival, while objective response rate describes a categorical tumor-response outcome. Neither endpoint measures exactly the same clinical course as the primary endpoint. Their results should therefore be considered alongside, rather than substituted for, the primary comparison.

Across the reported efficacy outcomes, the estimates are uncertain and do not establish a clear separation between the randomized groups. The secondary outcomes do not overturn the primary result; instead, they provide additional, differently defined views of the comparison. Numerical results for activity in crossover patients are not reported in the registry record, so that listed outcome cannot contribute a numerical comparison to the overall interpretation.

Multiple outcomes create a statistical interpretation issue. In general, when several hypotheses are tested, the chance of at least one apparently notable result can increase unless the analysis plan accounts for multiplicity. The registry does not report whether an adjustment or a hierarchy among secondary tests was prespecified. Consequently, secondary p-values should be given less weight than a clearly specified primary test, and isolated findings should be viewed cautiously. The outcome pattern is best read as descriptive supporting context, not as a collection of independent confirmations.

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

• Overall Survival
• Objective Response Rate
• Incidence of Adverse Events
• Activity (Overall Response Rate) in Crossover Patients

9. Statistical Interpretation

10. Statistical Methods Explained

How should the time-to-event analysis be read?

The Kaplan–Meier method estimates the pattern of event-free time over follow-up. For this trial, the event was disease progression or death from any cause. The median is a compact summary of that estimated pattern: it identifies the time at which the estimated event-free proportion reaches the midpoint. It does not describe every participant’s individual course, and it does not indicate that all participants experienced an event at the median time.

The log-rank test compares the event-time patterns between groups. The registry specifies a stratified log-rank test for the primary outcome and reports a hazard ratio for the comparison. In general, stratification accounts for specified grouping factors in the comparison. The factors used for this trial are not reported in the registry record. The sponsor-reported hazard ratio is the appropriate reported comparative estimate to quote; a simple recalculation from medians would not reproduce a time-to-event analysis.

What does the hazard ratio represent?

A hazard ratio summarizes a relative comparison of event rates over follow-up. A value of 1 represents equal rates in the comparison as coded; values on either side represent different relative rates. For this trial, the posted hazard ratio is 0.82, with a 95% confidence interval from 0.55 to 1.22. Because the interval includes 1, the estimate is not precise enough to rule out no difference under this measure. The reported p-value is 0.15. The registry labels the comparison as Arm I versus Arm II, but interpretation of which arm corresponds to the numerator depends on the analysis coding. The numerical estimate and its interval should therefore be read together with the stated arm order rather than as a standalone claim about direction.

How do confidence intervals and p-values complement each other?

In general, a confidence interval shows a range of effect estimates that are reasonably compatible with the observed data and the analysis assumptions. A p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis. Neither quantity gives the probability that the null hypothesis is true. The interval is especially useful for judging precision and the range of effects that remain plausible; the p-value is one summary of evidence against the null. For the primary outcome, the interval and p-value both reflect uncertainty about the difference between groups.

Why are other outcome methods different?

Overall survival is also a time-to-event outcome, and the registry reports medians and hazard ratio results for it. The same broad concepts apply, but overall survival has death as its event, rather than progression or death. Objective response rate is a binary outcome: each analyzed participant is categorized according to whether a response occurred within the stated timeframe. The registry reports group percentages and a sponsor analysis using the Cochran–Mantel–Haenszel method. This method compares categorical outcomes while accounting for strata, although the stratification details are not reported in the registry record.

A recalculated, unadjusted comparison of response rates is a different analysis from the sponsor’s reported Cochran–Mantel–Haenszel test. It is based on the posted group summaries and does not reproduce any stratified analysis. The two p-values therefore should not be treated as interchangeable. The registry’s reported analysis is the primary account of the sponsor’s result.

What can and cannot be inferred from the methods record?

The registry identifies randomization, double masking, a parallel-group design, Kaplan–Meier estimation, and a stratified log-rank test for the primary endpoint. It also gives the analysis population note that phase I lead-in patients were excluded from efficacy analysis. These details support a basic understanding of the comparison. However, the original statistical analysis plan, randomization implementation, stratification variables, missing-data procedures, and interim-analysis details are not reported in the registry record. It is therefore not possible to determine from the record whether additional model checks or sensitivity analyses were conducted.

In general, these methods answer different parts of the statistical question. The medians describe the estimated timing in each group; the hazard ratio summarizes the relative event-rate comparison; the confidence interval conveys precision; and the log-rank p-value summarizes evidence against the null comparison. No one measure should be read as a complete description of benefit, harm, or clinical importance.

11. Confidence Intervals and Precision

The primary hazard ratio was 0.82, with a 95% confidence interval from 0.55 to 1.22. The interval spans values below and above 1, the value corresponding to no relative difference in hazard. As a result, the reported estimate does not precisely pin down the direction or size of the comparative effect. The p-value of 0.15 is consistent with substantial uncertainty in this comparison.

The median progression-free survival estimates also have confidence intervals: 1.9 to 3.8 months for gemcitabine plus placebo, and 2.5 to 5.3 months for gemcitabine plus vismodegib. These intervals overlap. In general, overlapping intervals do not themselves constitute a formal test of the difference between medians; the reported log-rank comparison and hazard ratio address the group comparison using time-to-event information.

For a confidence interval, the stated confidence level describes the behavior of the interval-generating procedure over repeated use under its assumptions. It is not a probability statement that the particular interval contains the true effect. Wider intervals indicate less precision, while narrower intervals indicate greater precision. Precision depends on the amount and distribution of information available, but the registry does not provide enough details to attribute the observed width to particular causes.

The secondary outcomes also have uncertainty. For example, the posted response-rate intervals are broad, and the overall-survival hazard ratio interval includes 1. These results should be read as estimates with ranges of compatible values rather than as exact effects. A single point estimate can appear definitive when it is not; the confidence interval makes the remaining uncertainty visible.

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 time-to-event outcomes, the figures are total events required across the comparison. For other outcomes, they are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column describes the planned number of events or participants under which a study would have an 80% chance of detecting the specified effect, if that effect were the true one and the planning assumptions held. The 90% power column makes the corresponding calculation for a higher chance of detection. Neither column describes the chance that the treatment is effective, and these calculations are not observed power.

The rows that plan for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect ask how much information would be needed to detect effects of different sizes. Smaller effects are harder to distinguish from random variation, so they require more events or participants. The figures for time-to-event outcomes are especially important to read as event totals, not as participants per arm; the response-rate figures are participants per arm.

These planning illustrations are not a reconstruction of the trial’s design. The original sample-size justification and original planning assumptions are not reported in the registry record. The figures also depend on assumptions that may not match a future study. They should be used to understand how effect size and desired power relate to required information, not as evidence that the completed trial had a particular power.

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 = 0.820, so ln(HR) = -0.1985.
2. d = 4 × (1.96 + 0.842)² / [ln(0.820)]² = 797.2, rounded up to 798 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 <- 0.82                              # 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(1064622)
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 = 798 (80% power), 1,068 (90% power)
 75% of observed effect: events = 1,418 (80% power), 1,898 (90% power)
 50% of observed effect: events = 3,189 (80% power), 4,269 (90% power)
Simulated power with 798 events: 0.807 (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 1,123 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 118 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 <- 2.5          # control-arm median, months (converted from the posted unit)
hr          <- 0.82          # 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: 546         p (1-sided)   0.0001
  Events: 360        ~HR at bound   0.6763
    Month: 12    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.82   0.0338
    IA 2: 67%                   Z   2.5114
       N: 928         p (1-sided)   0.0060
  Events: 720        ~HR at bound   0.8293
    Month: 20    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.82   0.5603
        Final                   Z   1.9930
      N: 1124         p (1-sided)   0.0231
 Events: 1080        ~HR at bound   0.8858
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.82   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

For progression-free survival, the sponsor-reported hazard ratio was 0.82, with a 95% confidence interval from 0.55 to 1.22 and p = 0.15. This is the reported stratified log-rank analysis. The posted primary result does not identify a statistically significant difference between the randomized groups, and the interval leaves appreciable uncertainty about the effect.

For overall survival, the sponsor-reported hazard ratio was 0.96, with a 95% confidence interval from 0.64 to 1.46 and p = 0.37. The registry reports a Cochran–Mantel–Haenszel p-value of 0.42 for objective response rate. A simple unadjusted recalculation from the posted response counts gives p = 0.339. The latter uses a different approach and is not a substitute for the sponsor’s reported stratified analysis. The record does not flag a discrepancy for these results.

In general, a recalculation from summary counts cannot reproduce an analysis that accounts for stratification or uses a different model. It can serve as a check on the broad pattern, but the sponsor’s own reported analysis remains the relevant result for the stated method. The registry does not report enough methodological detail to independently reproduce the stratified analyses.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies progression-free survival as the primary endpoint and lists several secondary outcomes, including overall survival, objective response rate, adverse events, and activity among crossover patients. It does not report a multiplicity strategy, such as an adjustment across outcomes or an ordering that controls interpretation of secondary tests. In general, testing multiple outcomes raises the possibility of chance findings; without a stated strategy, secondary p-values are not equivalent to a single prespecified primary test.

The record says that phase I lead-in patients were not included in the efficacy analysis. It lists 53 participants in each randomized arm for the posted primary and secondary efficacy results. The registry does not report a complete analysis-population definition, such as whether the efficacy analysis followed intention-to-treat principles, nor does it describe exclusions after randomization. Those details should not be inferred from the arm counts alone.

Missing-data procedures are not reported in the registry record. For time-to-event outcomes, the record does not specify how incomplete follow-up, withdrawal, or other censoring situations were handled. For objective response rate, it does not describe the handling of participants without an evaluable response. The amount or pattern of missing outcome data is also not reported. These omissions limit assessment of whether missing information could affect the estimates.

Stratified methods are named for the primary comparison and for objective response rate, but the stratification factors are not reported. Details of the randomization sequence, allocation concealment, interim analyses, and the full statistical analysis plan are also not reported in the registry record. These are limits on what can be verified from the registry, not evidence that any particular procedure was or was not used.

17. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: vomiting (28.6%), abdominal pain (14.3%), ascites (14.3%), constipation (14.3%), death nos (14.3%).

In the randomized groups, serious adverse events affected 37 of 53 participants in the gemcitabine-and-placebo arm and 22 of 53 in the gemcitabine-and-vismodegib arm. Other adverse events affected 52 of 53 participants in each arm. These counts describe participants recorded as affected; they do not by themselves describe the number of events per participant, their duration, or their relationship to treatment.

The registry also lists serious adverse-event terms with percentages, including vomiting at 28.6%, and abdominal pain, ascites, constipation, death NOS, and dehydration at 14.3% each. The record does not give enough context in the available information to infer the severity or course of each listed event beyond its classification as serious. Phase I lead-in and crossover patients are reported separately, and their counts should not be combined with the randomized-arm figures when interpreting the randomized comparison.

Safety counts are not a randomized comparison of risk-adjusted effects unless analyzed with appropriate methods. The record does not report a formal comparative safety analysis or deaths by randomized group. These figures describe recorded adverse events and should be read alongside the efficacy outcomes, not as a complete measure of overall benefit or harm.

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

The posted primary result describes median progression-free survival of 2.5 months with gemcitabine plus placebo and 4.0 months with gemcitabine plus vismodegib. The reported hazard ratio was 0.82, with a 95% confidence interval from 0.55 to 1.22 and p = 0.15. Taken together, these statistics do not establish a clear difference between the randomized groups. The confidence interval leaves uncertainty about the comparative effect, including the possibility of little or no difference.

This result does not prove that the treatments have identical effects. A non-significant p-value is not evidence of equivalence, and no equivalence margin is reported in the registry record. Nor does the result establish that a difference, if present, is clinically important. The record does not specify a threshold for clinical importance.

The trial’s results apply to the analyzed groups and the methods recorded for this study. They do not automatically describe every patient with pancreatic cancer or other treatment settings. The registry describes a phase II randomized study, and phase I lead-in patients were excluded from efficacy analysis. It also allowed crossover after progression for patients initially assigned to gemcitabine and placebo, which is relevant context for interpreting outcomes that occur after progression.

Overall survival, response, and adverse events offer additional information but answer different questions. A pattern across several outcomes can help frame the evidence, but secondary outcomes should not be treated as independent confirmation when multiplicity handling is not reported. The record also does not provide enough detail about missing-data methods, analysis populations, or the full statistical plan to resolve every concern about robustness.

These statistics are evidence about a group comparison in a trial, not individualized medical guidance. They should be interpreted as estimates with uncertainty, alongside the study design and the limitations of what the registry reports.

19. Why This Trial Matters Statistically

This trial illustrates why an estimated difference and the strength of evidence for that difference are not the same thing. The median progression-free survival estimates differ, while the reported hazard ratio has a confidence interval that includes 1 and a p-value of 0.15. Reading only the medians would omit uncertainty about the comparison; reading only the p-value would omit the range of effects compatible with the data.

It also shows why time-to-event endpoints require their own methods. Kaplan–Meier estimation and a log-rank comparison use event timing and follow-up information, rather than reducing the result to a simple count at one time point. The hazard ratio adds a relative summary, but its direction must be read in light of the arm order and analysis coding.

The randomized, double-blind, placebo-controlled design provides a structured comparison of assigned treatments. At the same time, the crossover option and the exclusion of phase I lead-in patients from efficacy analysis are important features of how the results should be understood. The record’s secondary outcomes and safety counts broaden the evidence, but multiplicity and limited reporting of analysis details constrain how much weight individual findings can carry.

Finally, the planning illustrations demonstrate that the information required to detect smaller effects rises as the target effect becomes smaller. They are not a substitute for the trial’s original design rationale, which is not reported in the registry record. Together, these features make the study useful for understanding how design, endpoint choice, estimation, and uncertainty shape interpretation of a clinical trial result.

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 registry record gives important design and result details but leaves several trial-specific uncertainties. The primary analysis is described as stratified, yet the stratification factors are not reported. The original statistical analysis plan, sample-size justification, randomization implementation, and any interim analyses are also not reported in the registry record. This limits independent assessment of the prespecified analysis and its implementation.

The record states that phase I lead-in patients were excluded from efficacy analysis and reports 53 participants in each randomized arm for the efficacy outcomes. It does not fully describe the analysis population or explain whether all randomized participants were analyzed according to initial assignment. Missing-data and censoring procedures are not reported, and the response outcome’s approach to participants without evaluable assessments is not stated.

Crossover was permitted for participants assigned to gemcitabine and placebo after progression and unblinding. The registry does not describe how crossover was handled for overall survival or other analyses after progression. This limits interpretation of outcomes that may be affected by post-randomization treatment.

The registry also does not report a multiplicity plan for the secondary outcomes or a clinical-importance threshold for the primary result. Numerical activity results for crossover patients are not reported in the registry record. These limits do not demonstrate that the analyses were inappropriate; they indicate that the available record does not allow those aspects to be evaluated. The estimates should therefore be interpreted with their stated confidence intervals and with caution about details that are not documented.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Gemcitabine Hydrochloride With or Without Vismodegib in Treating Patients With Recurrent or Metastatic Pancreatic Cancer — NCT01064622.
• Registry record last updated 2024-11-19; status last verified 2017-10.
• Results first posted 2015-02-13.
• 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

This completed randomized, double-blind, parallel-group phase II trial compared gemcitabine hydrochloride plus placebo with gemcitabine hydrochloride plus vismodegib in recurrent or metastatic pancreatic cancer. Enrollment was 118. The registry reports 53 participants in each randomized arm for the efficacy outcomes and excludes phase I lead-in patients from efficacy analysis.

Progression-free survival was the primary endpoint, defined as time from randomization to disease progression or death from any cause. The reported hazard ratio was 0.82, with a 95% confidence interval from 0.55 to 1.22 and p = 0.15. The registry also reports overall survival, objective response rate, and adverse-event results. Crossover after progression was permitted in the placebo arm. Several details of the original statistical plan, missing-data handling, and multiplicity procedures are not reported in the registry record.