Study of Regorafenib as a 3rd-line or Beyond Treatment for Gastrointestinal Stromal Tumors (GIST): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Regorafenib as a 3rd-line or Beyond Treatment for Gastrointestinal Stromal Tumors (GIST) (NCT01271712), a randomized phase 3 study. The primary outcome is Progression-free Survival.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled phase III study with a parallel-group design and quadruple masking recorded in the registry. Bayer was the sponsor. The study concerned regorafenib plus best supportive care compared with placebo plus best supportive care for gastrointestinal stromal tumors that were metastatic and/or unresectable after progression despite at least imatinib and sunitinib.

The record reports enrollment of 199. The primary analysis population was the Full Analysis Set, defined as all randomized participants. The primary endpoint results list 133 participants in the regorafenib arm and 66 in the placebo arm. The study included screening, treatment, and survival follow-up periods. Participants entered survival follow-up after stopping randomized study treatment.

The described regorafenib schedule was 160 mg orally once daily for 3 weeks of each 4-week cycle, followed by a week off. Placebo participants received matching tablets on the same schedule. Best supportive care was part of both randomized groups. The record says it excluded disease-specific anticancer therapies such as kinase inhibitors, chemotherapy, radiation therapy, or surgery during the described randomized treatment.

Tumor assessments were planned every 4 weeks for the first 3 months, every 6 weeks for the next 3 months through month 6, and every 8 weeks thereafter until treatment ended, with more frequent assessments possible when clinically indicated. Assessments used CT or MRI and continued until progression was seen in central radiology review. After progression, placebo participants could be offered active treatment, while participants progressing during regorafenib could continue open-label treatment. Those arrangements matter when interpreting outcomes after progression, particularly overall survival.

4. Participant Flow and Accounting

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

Before assignment: Participants were randomized in a 2:1 ratio to receive either regorafenib (133 patients) or placebo (66 patients). Randomization was stratified according 3rd vs. 4th line of therapy (at least 50% of patients were to be 3rd line), and geographical region (Asia vs.rest of world).

Double Blind Treatment

Reasons for not completing this period:

Open Label Treatment

Reasons for not completing this period:

Safety Follow-up

Reasons for not completing this period:

Survival Follow-up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) - defined as all randomized participants.

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 From randomization of the first subject until approximately 144 progression-free survival events had occurred (study duration approximately one year).

Progression-free survival (PFS) was the primary endpoint. It measured the time from randomization to the first of radiological disease progression or death from any cause. Progression was determined by central radiological assessment using modified RECIST v.1.1. The record defines progression through an increase in the sum of target-lesion diameters relative to the smallest sum on study, unequivocal progression of existing non-target lesions, or the appearance of new lesions.

A time-to-event endpoint uses information about both whether an event occurred and when it occurred. It can incorporate participants whose follow-up ends before an event is observed, rather than treating their observed follow-up as if it were the event time. For this analysis, participants without progression or death at the analysis time were censored at their last tumor evaluation. Censoring indicates that an event had not been observed by the last recorded evaluation; it does not establish what happened afterward.

PFS is used to describe how long participants remain alive without recorded progression under the endpoint definition. It is distinct from overall survival, which concerns death, and from tumor response, which concerns response status. The registry identifies the primary analysis population as all randomized participants. The posted results give median PFS and a Cox hazard ratio, allowing the groups to be described both by their event-time distributions and by a relative time-to-event comparison.

As a general statistical point, PFS can provide information about disease progression before survival follow-up is complete. Its interpretation still depends on how progression is assessed, the handling of censoring, and the analysis population. The registry record describes central assessment and the censoring rule, but does not report further details about missing assessments or the full statistical plan.

7. Results Posted in the Registry

• Regorafenib (Stivarga, BAY73-4506) vs Placebo: hazard ratio 0.27 (95% CI 0.18–0.39) (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: 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:
  • Regorafenib (Stivarga, BAY73-4506): 82.0% (109/133) versus 80.3% (53/66) on control; risk difference 1.7 percentage points (95% CI -10.0 to 13.3), risk ratio 1.02 (0.88–1.18); unadjusted two-proportion z-test p = 0.778.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Regorafenib (Stivarga, BAY73-4506) and the control. The interval gives the range of effects that remain compatible with the data.

Time to Progression (TTP)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Regorafenib (Stivarga, BAY73-4506) vs Placebo: hazard ratio 0.25 (95% CI 0.17–0.36) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Regorafenib (Stivarga, BAY73-4506) vs Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

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:
  • Regorafenib (Stivarga, BAY73-4506): 4.5% (6/133) versus 1.5% (1/66) on control; risk difference 3.0 percentage points (95% CI -1.6 to 7.6), risk ratio 2.98 (0.37–24.23); unadjusted two-proportion z-test p = 0.280.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Regorafenib (Stivarga, BAY73-4506) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes give a broader view of tumor control and survival, but they do not all answer the same question. Time to progression is another time-to-event measure focused on progression. Overall survival concerns death, while objective response concerns the proportion meeting a response definition. The registry also names tumor response, disease control rate, and duration of response among the secondary outcomes, but the number of posted outcome measures and analyses does not mean every listed endpoint has a complete result in the record.

At a broad level, the time-to-progression comparison points in the same direction as the primary PFS result. The overall-survival comparison is less conclusive by its reported confidence interval, and the response comparison is imprecise. These differences are not inherently contradictory: endpoints measure different events, are affected by different follow-up patterns, and can have different statistical precision. PFS includes progression or death, while overall survival concerns death; tumor response is a separate outcome and may be observed in relatively few participants.

Secondary outcomes generally carry less evidential weight when multiple outcomes are examined and the record does not report how multiplicity was addressed. When many hypotheses are tested, the chance of at least one apparently notable result can rise. An adjustment or prespecified hierarchy can address this concern, but the registry record does not report a multiplicity plan. The secondary outcomes can therefore support context and identify patterns, but should not be treated as independent confirmations of the primary result or as definitive evidence based only on nominal comparisons.

Post-progression treatment options are also relevant when relating progression outcomes to survival. Placebo participants who progressed could be offered active treatment, and participants progressing during regorafenib could continue open-label treatment. Such treatment after progression can affect later outcomes and makes a simple reading of overall survival as an isolated comparison of randomized treatment exposure incomplete. The registry record does not report a detailed analysis of these pathways.

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

• Overall Survival
• Time to Progression (TTP)
• Tumor Response
• Objective Response Rate
• Disease Control Rate (DCR)
• Duration of Response (DOR)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome. Each participant contributes a time from randomization until progression or death, if observed, or until censoring if neither event was recorded by the last tumor evaluation. The median summarizes the center of the estimated event-time distribution. The reported median values are 147 days for regorafenib and 28 days for placebo. Their confidence intervals are 122 to 173 days and 28 to 32 days, respectively.

What does a hazard ratio describe?

The registry reports a Cox regression hazard ratio of 0.268 for regorafenib versus placebo, with a 95% confidence interval of 0.185 to 0.388. In general, a hazard is an event rate at a particular point in follow-up among participants who have not yet had the event. A hazard ratio compares those rates between groups over time. A value below 1 points to a lower estimated hazard in the first-named group, subject to the model and analysis conditions. It does not mean that the event probability is reduced by the same proportion, and it does not directly compare the groups’ medians.

The Cox model uses the ordering and timing of events and can include censored participants. Its usual interpretation as one summary ratio over follow-up relies on a proportional-hazards assumption: broadly, that the relative hazards are adequately represented by a constant ratio. The registry record does not report whether that assumption was assessed, what covariates were included in the regression, or the full model specification. Those details should not be inferred from the term “Regression, Cox” alone.

Why is a log-rank analysis also listed?

The registry lists a log-rank analysis for the primary comparison, as well as the Cox regression analysis. In general, the log-rank test compares the event-time experience of groups across follow-up while accounting for censoring. It produces a test of evidence against equal event-time distributions under its assumptions; it does not itself provide a magnitude of effect. The Cox hazard ratio gives a relative-effect estimate, while the medians give an absolute time scale. The registry record does not report further details of the log-rank specification.

How should censoring be understood?

The primary description says that participants without progression or death at analysis were censored at their last tumor evaluation. Censoring is a statistical way to retain the follow-up observed up to that point without claiming that the event happened then. Standard time-to-event methods rely on assumptions about censoring, including that the censoring process does not systematically hide different event risks in a way that distorts the comparison. The record does not report detailed information about reasons for censoring, missing tumor assessments, or diagnostic checks for those assumptions.

Central radiological assessment was used for PFS, with modified RECIST v.1.1. This provides a specified basis for defining and assessing progression. It does not remove all measurement uncertainty, and the record does not give further information about adjudication procedures or agreement between assessments. Death from any cause was included as an event, so PFS combines radiological progression and death rather than isolating either component.

The Full Analysis Set is defined as all randomized participants. This identifies the primary population, but the registry record does not provide a detailed account of every participant’s analysis status, exclusions, or missing endpoint data. The enrollment figure and arm counts are descriptive record entries and should not be used to infer unreported analysis details.

For binary outcomes such as objective response and the reported percentage of participants with death, group percentages describe the observed proportions at the relevant analysis. A risk difference is the first group’s proportion minus the comparator’s proportion in the recalculation. Its confidence interval expresses uncertainty in that difference. A confidence interval spanning zero is compatible with no difference under that interval procedure; it also allows values in either direction. A test result or interval alone does not establish that two groups are equivalent.

For overall survival and objective response, the posted recalculations are unadjusted comparisons of summary statistics. They are not substitutes for a sponsor’s full analysis, which may use methods that account for time-to-event follow-up or other features of the trial. The registry reports a Cox hazard ratio and log-rank result for overall survival, but no reported analysis for objective response in the listed results. The record does not describe adjustment for multiple endpoint testing.

In general, over-dispersion refers to variability greater than a statistical model expects. It can make standard errors too small if ignored. The registry record does not report an over-dispersion analysis for these outcomes, and the primary time-to-event results should not be described as if such a model were used. More broadly, a named method does not reveal every modeling decision; interpretation should remain within the details recorded.

11. Confidence Intervals and Precision

Confidence intervals communicate uncertainty in an estimate under the statistical method used. A 95% confidence interval is not a range containing 95% of individual outcomes. In repeated use of the same method under its assumptions, intervals constructed this way would cover the underlying parameter at the stated rate. For an individual trial result, the interval indicates which parameter values are reasonably compatible with the data and method, rather than providing certainty about one exact value.

For the primary PFS medians, the reported intervals are 122 to 173 days for regorafenib and 28 to 32 days for placebo. The Cox hazard ratio is 0.268, with a 95% confidence interval from 0.185 to 0.388. The interval lies below 1, so the range of values compatible with this estimate under the reported interval method points toward a lower hazard in the regorafenib group. The interval does not quantify individual benefit, and it does not remove uncertainty about model assumptions or endpoint measurement.

For overall survival, the sponsor-reported Cox hazard ratio is 0.909 with a 95% confidence interval from 0.653 to 1.265. This interval includes 1, the value corresponding to equal hazards. The recalculated risk-difference interval also spans zero. These intervals allow a range of effects in either direction; they do not establish equivalence or prove that there is no difference.

For objective response, the posted arm-specific confidence intervals are 1.7% to 9.6% and 0.0% to 8.2%. The recalculated difference interval spans zero. The breadth of these intervals signals substantial uncertainty in the size and direction of the difference. In general, precision depends on the amount and distribution of information, not only on the point estimate. Precision should therefore be judged from the interval alongside the endpoint and analysis method, not from a single estimate alone.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on observed effects, not the trial’s original design assumptions. The stated illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. For the time-to-event outcomes, the figures are total events needed, using the Schoenfeld approach. For the other outcomes, the figures are participants per arm.

The 80% power column describes the planning number of events or participants associated with an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions were true. The 90% power column uses a higher chance of detection and therefore requires more information. The rows for 100%, 75%, and 50% of the observed effect illustrate how the planning target changes when the assumed effect is smaller than the observed estimate. Smaller effects need more participants or events to distinguish them from random variation with the same power and significance level.

For time-to-event outcomes, event counts are not participant counts: participants may be censored without an event, and the timing of events is relevant to the analysis. For binary outcomes, the figures are participants per arm, not a total across arms. The planning display is not observed power. It does not describe the probability that this completed trial’s result is true, and it is not a retrospective judgment of the trial’s success. The registry record does not report the original sample-size justification or the assumptions used in the trial’s own design.

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 = 0.268, so ln(HR) = -1.3168.
2. d = 4 × (1.96 + 0.842)² / [ln(0.268)]² = 18.1, rounded up to 19 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 <- 0.268                              # 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(1271712)
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 = 19 (80% power), 25 (90% power)
 75% of observed effect: events = 33 (80% power), 44 (90% power)
 50% of observed effect: events = 73 (80% power), 97 (90% power)
Simulated power with 19 events: 0.803 (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 26 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 199 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 <- 0.920547945205479          # control-arm median, months (converted from the posted unit)
hr          <- 0.268          # 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: 12         p (1-sided)   0.0001
  Events: 9        ~HR at bound   0.0741
  Month: 11    P(Cross) if HR=1   0.0001
            P(Cross) if HR=0.27   0.0338
  IA 2: 67%                   Z   2.5114
      N: 20         p (1-sided)   0.0060
 Events: 17        ~HR at bound   0.2877
  Month: 19    P(Cross) if HR=1   0.0060
            P(Cross) if HR=0.27   0.5603
      Final                   Z   1.9930
      N: 26         p (1-sided)   0.0231
 Events: 25        ~HR at bound   0.4461
  Month: 60    P(Cross) if HR=1   0.0250
            P(Cross) if HR=0.27   0.9000



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

15. Analyses Reported by the Sponsor

The sponsor’s posted primary analysis reports a Cox hazard ratio of 0.268 with a 95% confidence interval of 0.185 to 0.388 for PFS. The same hazard-ratio estimate and interval are recorded in the results, so the interpretation of the primary time-to-event comparison is anchored in the sponsor-reported analysis. The record also lists a log-rank analysis for PFS.

For overall survival, the sponsor-reported Cox analysis gives a hazard ratio of 0.909 and a 95% confidence interval of 0.653 to 1.265. The posted results also include a log-rank analysis. The recalculated overall-survival risk difference is an unadjusted comparison of the posted group-level proportions; it is not the same estimand or method as the Cox hazard ratio. Its interval and p-value should not replace the sponsor’s time-to-event analysis.

The registry lists no sponsor-reported analysis for objective response in the results. Any recalculated comparison of that binary outcome is therefore a simple unadjusted analysis of the posted summary statistics, rather than a reconstruction of an analysis plan. The registry record does not report the original statistical analysis plan in enough detail to determine whether other adjustments or models were used. No discrepancy is recorded between the primary posted estimate and its sponsor analysis. Where a sponsor analysis is reported, it remains the relevant trial analysis rather than being displaced by a simple recalculation.

16. Multiplicity, Missing Data and Analysis Populations

The registry record identifies PFS as the primary endpoint and lists several secondary outcomes, including overall survival, time to progression, tumor response, objective response rate, disease control rate, and duration of response. It does not report a multiplicity-adjustment strategy, a hierarchy for testing endpoints, or whether particular secondary analyses were designated confirmatory. Without that information, secondary p-values should be interpreted cautiously: repeated testing can increase the chance of a nominally unusual result even when there is no corresponding effect.

The primary population is defined as the Full Analysis Set, meaning all randomized participants. The record does not provide further detail about the analysis population for each secondary outcome, the handling of participants without an evaluable assessment, or the quantity and reasons for missing data. For PFS, it states that participants without progression or death at analysis were censored at their last tumor evaluation. This specifies how that circumstance was treated in the time-to-event description, but it does not provide a full account of missingness or censoring patterns.

The registry record does not report whether interim analyses were planned or conducted, the original sample-size justification, the complete statistical analysis plan, or detailed model diagnostics. These items should not be inferred from the phase, enrollment, or the methods named in the results. The planning illustrations are distinct from the trial’s original design assumptions.

There are also treatment pathways after progression: placebo participants could be offered active treatment, and participants progressing during regorafenib could continue open-label treatment. The record does not describe how post-progression treatment was handled in the overall-survival analysis. This limits what can be concluded about the relationship between randomized assignment and later survival, even though the randomized comparison remains the basis of the reported analysis. The record’s lack of further detail is a reporting limitation, not evidence that a particular procedure was or was not used.

17. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death nos (25.0%), nausea (12.5%), fatigue (12.5%), non-cardiac chest pain (12.5%), general disorders and administration site conditions - other (12.5%).

The adverse-event summary separates several exposure groups: double-blind regorafenib, double-blind placebo, placebo followed by open-label treatment, regorafenib at any time, and regorafenib for more than 1 year. For each listed group, the record gives the number at risk and the number affected for serious events, other events, and deaths. These are group-specific counts and should be read with the corresponding group definition, not combined into a randomized-arm comparison.

The categories represent different treatment-exposure histories and may not be mutually exclusive. In particular, “regorafenib at any time” and longer-duration regorafenib describe exposure across treatment periods, while the double-blind groups describe a different period. The registry record does not provide enough detail to turn these summaries into a causal comparison of safety between the randomized assignments. The counts also do not by themselves show event timing, severity grading beyond the serious-event classification, duration, or whether an event was judged treatment-related.

The listed serious-event terms include Death NOS at 25.0%, with Nausea, Fatigue, Non-cardiac chest pain, General disorders and administration site conditions - Other, and Hepatobiliary disorders - Other each listed at 12.5%. These labels and percentages are a record summary, not evidence that the events were caused by a study treatment. Death counts in the adverse-event summary should not be substituted for the defined overall-survival analysis.

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

The primary endpoint results describe a randomized comparison of PFS in participants with metastatic and/or unresectable gastrointestinal stromal tumors whose disease had progressed despite at least imatinib and sunitinib. The posted medians and Cox hazard ratio favor the regorafenib group in the time-to-event comparison. This is a statement about the observed group-level analysis and its estimated relative event rate, not a guarantee of an outcome for any individual.

The result does not mean that every participant in the regorafenib group remained progression-free longer than every participant in the placebo group. Medians summarize distributions, and participants’ individual disease courses can differ. The hazard ratio is not a direct measure of the probability of benefit, an absolute risk difference, or a ratio of the two medians. The confidence interval describes statistical uncertainty under the reported method and assumptions; it does not account for every possible source of bias or measurement error.

The primary outcome combines radiological progression and death from any cause. It does not isolate the contribution of either event type. It also does not, by itself, establish an overall-survival effect. The posted overall-survival comparison is less precise, and its Cox confidence interval includes 1. The secondary response result is another distinct measure and should not be treated as interchangeable with PFS.

The comparator and treatment context matter. Both randomized groups received best supportive care, and the study involved participants with prior treatment progression. Placebo participants could be offered active treatment after progression, and regorafenib participants could continue open-label treatment after progression. Those options mean that outcomes after progression are not simply a comparison of continued blinded treatment in the original groups.

The findings apply to the trial population and the reported analysis period. The registry record does not establish how the results generalize to people outside that population or to treatment contexts not described. Nothing in these statistical results is individual medical advice or a substitute for clinical judgment.

19. Why This Trial Matters Statistically

Statistically, this trial illustrates why a primary endpoint should be read through its definition and analysis, not just its headline estimate. PFS combines radiological progression and death, uses central assessment, and specifies how participants without an observed event were censored. Those details define what the reported medians and hazard ratio represent.

It also demonstrates that different summaries answer different questions. The median gives a time-scale summary of each group’s event experience; the Cox hazard ratio compares relative event rates over follow-up; and confidence intervals express uncertainty around estimates. None is a replacement for the others. Their interpretation depends on the endpoint and modeling assumptions, some of which are not detailed in the registry record.

The secondary outcomes show why statistical evidence should be considered as a pattern rather than a collection of isolated results. Time to progression is directionally consistent with the primary endpoint, whereas the overall-survival interval is compatible with a range of effects. Response outcomes are imprecise, and the record does not report multiplicity handling. These features are important when deciding how much weight to place on secondary comparisons.

The study’s treatment pathways after progression also make the distinction between progression outcomes and later survival especially relevant. Active or open-label treatment could follow progression, so the survival comparison reflects more than the blinded treatment period alone. Finally, the registry’s level of detail sets limits: the full statistical plan, original design assumptions, missing-data details, and interim-analysis information are not reported. Careful statistical reading includes recognizing both the strength of the primary comparison and the boundaries of what the record supports.

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.

Several limitations are specific to the information recorded for this study. The registry identifies central radiological assessment and modified RECIST v.1.1 for PFS, but does not report further details about adjudication, assessment agreement, or missing tumor evaluations. It gives a censoring rule for participants without progression or death, but not the distribution or reasons for censoring. The assumptions that support time-to-event analyses therefore cannot be fully assessed from the record.

The record does not report the complete statistical analysis plan, original sample-size justification, interim-analysis details, Cox model specification, or checks of proportional hazards. It also does not report a multiplicity strategy for the several secondary outcomes. These omissions limit evaluation of prespecification, model choices, and the evidential status of secondary comparisons.

Post-progression treatment options complicate interpretation of outcomes after progression. Placebo participants could be offered active treatment, and regorafenib participants could continue open-label treatment. The registry does not report how these treatment histories were incorporated into the overall-survival analysis. This is particularly relevant when interpreting overall survival as a comparison based on randomized assignment.

The adverse-event record uses groups defined by treatment period or exposure history, including participants treated with regorafenib at any time and for more than 1 year. These are not simple randomized-arm safety comparisons. The available summary does not supply enough detail about event timing, attribution, or participant-level overlap to interpret the counts as causal treatment effects.

Finally, the posted results concern a specific population with disease progression after prior imatinib and sunitinib. The record does not establish generalizability beyond that setting. These limitations qualify the scope of interpretation; they do not by themselves negate the reported primary comparison.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Regorafenib as a 3rd-line or Beyond Treatment for Gastrointestinal Stromal Tumors (GIST) — NCT01271712.
• Registry record last updated 2021-01-29; status last verified 2021-01.
• Results first posted 2013-10-25.
• 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.

24. Record Summary

The registry describes a randomized, double-blind, placebo-controlled phase III parallel-group study of regorafenib plus best supportive care versus placebo plus best supportive care in metastatic and/or unresectable gastrointestinal stromal tumors after progression despite at least imatinib and sunitinib. Enrollment was 199, and the primary population was the Full Analysis Set, defined as all randomized participants.

The primary endpoint was PFS, defined as time from randomization to radiological progression or death from any cause, based on central radiological assessment. The posted medians were 147 days for regorafenib and 28 days for placebo; the sponsor-reported Cox hazard ratio was 0.268 with a 95% confidence interval of 0.185 to 0.388.

The registry also lists overall survival, time to progression, and response outcomes. Secondary results are not equally precise, and the record does not report a multiplicity plan, full statistical analysis plan, or original sample-size justification. Treatment could change after progression, which is relevant to interpreting later survival and safety summaries.