Patients With Metastatic Colorectal Cancer Treated With Regorafenib or Placebo After Failure of Standard Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Patients With Metastatic Colorectal Cancer Treated With Regorafenib or Placebo After Failure of Standard Therapy (NCT01103323), a randomized phase 3 study. The primary outcome is Overall Survival.

2. Clinical Question

The clinical question concerns a treatment strategy added to best supportive care in a population whose cancer had progressed after standard therapy. It is not a comparison of regorafenib with supportive care alone: both groups received best supportive care, and the comparator also received matching placebo tablets. Randomization supports a between-group comparison under the trial’s assigned treatment strategies, while masking was intended to limit knowledge of assignment; the registry does not identify who was masked.

Overall survival is the primary endpoint, with progression-free survival, objective tumor response, disease control, and tumor response listed among secondary outcomes. The results therefore address more than one kind of outcome: time until an event, tumor assessments, and safety observations. Those measures answer related but distinct questions. The trial record does not establish that the results apply to people outside the described population or to treatment settings other than the regimens recorded.

3. Trial Design

The registry describes a randomized, double-blind, placebo-controlled, multicenter phase III study using a parallel-group design. It lists enrollment of 760 and identifies Bayer as sponsor. The record gives the study start as 2010-04, primary completion as 2011-07, and status as completed. The posted primary outcome is overall survival in the intent-to-treat population.

Participants were assigned to regorafenib plus best supportive care or matching placebo plus best supportive care. The regorafenib regimen was 160 mg by mouth once daily for 3 weeks on and 1 week off in each 4 week cycle. The placebo regimen followed the same schedule, and both arms included best supportive care. The registry records quadruple masking as well as double-blind in the study description; it does not specify the roles covered by the quadruple-masking designation.

The primary endpoint timeframe is described as running from randomization of the first subject until a database cut-off approximately 14 months later, 19May2010 - 21Jul2011, used for the 2nd planned formal interim analysis. This wording gives the record’s analysis context, but does not supply the full monitoring or analysis plan. Original sample-size justification, allocation ratio assumptions in the protocol, details of randomization implementation, and the planned handling of multiplicity are not reported in the registry record.

Posted primary arm counts are 505 for regorafenib plus best supportive care and 255 for placebo plus best supportive care. These are the counts associated with the displayed outcome results; the registry’s overall enrollment entry is 760. The record does not explain the relationship between the enrollment entry and the outcome-specific counts, so those entries should be read as reported rather than reconciled by assumption.

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.

Without/Before Drug Switch

Reasons for not completing this period:

Switched From Placebo to Regorafenib

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat (ITT)

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival, measured over From randomization of the first subject until the database cut-off approximately 14 months later (19May2010 - 21Jul2011) used for 2nd planned formal interim analysis (IA)..

Overall survival is defined in the registry as the time in days from randomization to death due to any cause. Participants alive at analysis were censored at the last date known to be alive. A participant lost to follow-up with no contact after randomization was censored at Day 1. The endpoint therefore combines follow-up time and the occurrence of death, while censoring records the last point at which a participant’s survival status contributes information.

Overall survival is used because it measures time to an outcome that does not depend on tumor-response judgment or a particular cause of death. In general, a time-to-event endpoint can use information about both whether an event occurred and when it occurred; participants without a recorded event by the analysis cut-off can still contribute follow-up until censoring. That feature can make the endpoint informative when follow-up times differ, but interpretation depends on how follow-up and censoring were handled.

The registry reports the median overall survival for each group and a hazard ratio from a log-rank comparison. A median describes the point by which half of the relevant survival distribution has experienced the event, as estimated in the analysis. It does not describe every participant’s experience or the full shape of survival over time. The hazard ratio addresses the relative event hazard over follow-up under the model or comparison used; it is not a direct difference in median survival. The record does not report additional survival-curve summaries in the registry record described for this analysis.

7. Results Posted in the Registry

• Regorafenib (Stivarga, BAY73-4506)+BSC vs Placebo+BSC: hazard ratio 0.77 (95% CI 0.64–0.94), reported p = 0.005 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Progression-free Survival (Based on Investigator's Assessment)

• 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:
  • Regorafenib (Stivarga, BAY73-4506)+BSC vs Placebo+BSC: hazard ratio 0.49 (95% CI 0.42–0.58), reported p < 0.001 (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)+BSC vs Placebo+BSC than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Objective Tumor Response

• 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)+BSC: 1.0% (5/505) versus 0.4% (1/255) on control; risk difference 0.6 percentage points (95% CI -0.6 to 1.8), risk ratio 2.52 (0.30–21.50); unadjusted two-proportion z-test p = 0.379.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Regorafenib (Stivarga, BAY73-4506)+BSC and the control. The interval gives the range of effects that remain compatible with the data.

Disease Control

• 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)+BSC: 41.0% (207/505) versus 14.9% (38/255) on control; risk difference 26.1 percentage points (95% CI 20.0 to 32.2), risk ratio 2.75 (2.01–3.76); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Regorafenib (Stivarga, BAY73-4506)+BSC than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several aspects of disease course. The posted progression-free survival comparison is a time-to-event analysis based on investigator assessment, with tumor assessment at 8 week intervals. Objective tumor response and disease control are categorical measures, also assessed at those intervals. Together, these outcomes provide context about tumor status and progression alongside the primary overall survival endpoint, but they do not measure the same event or time scale.

Across the secondary results, the progression-free survival hazard-ratio direction and disease-control percentages align with the direction of the primary overall survival comparison. Objective tumor response was uncommon in both groups, and the sponsor’s reported comparison does not provide clear evidence of a between-group difference. These statements describe the broad pattern rather than establish that the secondary outcomes independently confirm the primary finding. Endpoint definitions, investigator assessment, follow-up, and analysis methods all affect how the outcomes relate.

Secondary outcomes generally carry less inferential weight when multiple outcomes are examined and the registry does not report how multiplicity was addressed. Testing many outcomes can increase the chance of at least one apparently notable result if no adjustment or hierarchy is used. The record lists secondary outcomes and analyses but does not report a multiplicity strategy, testing hierarchy, or adjusted significance thresholds. Accordingly, isolated secondary p-values should be interpreted cautiously and in the context of the primary result and the full outcome set.

The posted estimates can still be informative descriptively. They indicate what the trial recorded for each endpoint and how the between-group pattern compares with the primary outcome. They are not proof of a mechanism, do not establish that changes in tumor measures account for the overall survival result, and do not replace the primary endpoint. The registry record does not report mediation analyses or other evidence linking changes in secondary outcomes to overall survival.

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

• Progression-free Survival (Based on Investigator's Assessment)
• Objective Tumor Response
• Disease Control
• Tumor Response

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result is a time-to-event comparison. The registry defines the event as death from any cause and measures time from randomization. Participants alive at the analysis date were censored at the last date known to be alive; for someone lost to follow-up with no contact after randomization, censoring was assigned at Day 1. Censoring is not itself an event. It marks the point after which the record does not establish whether the event occurred during observed follow-up.

What does the median describe?

A median survival time is a location summary for the estimated survival distribution. It indicates the time by which the estimated proportion experiencing the event reaches the midpoint. It is useful because it gives an interpretable time scale, but it does not say that every participant experienced the event at that time. It also does not show how the groups compare at every time point. The primary outcome reports medians in days with 95% confidence intervals.

What does the hazard ratio describe?

A hazard is the instantaneous event rate among participants still at risk at a particular time. A hazard ratio compares the hazards between groups, with the direction depending on the order of the comparison and the event definition. Here, the reported contrast is regorafenib plus best supportive care versus placebo plus best supportive care, and the event is death. A ratio below 1 is therefore directionally consistent with a lower estimated death hazard in the regorafenib group during the analyzed follow-up. It is not a ratio of medians, a probability of survival, or a direct statement about an individual participant.

The registry reports the hazard ratio using a log-rank method. In general, the log-rank test compares observed event patterns across groups over follow-up, taking account of the timing of events and censoring. It produces evidence about whether the groups’ event-time distributions differ under the tested comparison. The registry’s p-value is not the probability that the null hypothesis is true, nor does it measure the size or importance of the difference. Interpretation of a hazard ratio as a stable relative effect over follow-up also depends on assumptions about how hazards behave; the relevant diagnostic results are not reported in the registry record.

How should the confidence interval and p-value be read?

A confidence interval expresses uncertainty around an estimated quantity under the statistical procedure used. For the hazard ratio, the interval gives a range of values compatible with the data and analysis at the stated confidence level. It is not a guarantee that the true value lies in the interval, and it does not include every source of uncertainty, such as limitations in the registry record or possible bias. The p-value summarizes how unusual the observed data or more extreme data would be under a specified null model and its assumptions. It should be considered alongside the estimate and interval, not used as a substitute for them.

The posted primary estimate and p-value are the sponsor’s reported log-rank results. The time-to-event estimates are not independently recalculated from the medians, because medians and their intervals do not provide enough information to reconstruct the hazard ratio. This distinction matters: an unadjusted recalculation from summary data, where available for other endpoint types, is not interchangeable with the sponsor’s analysis.

Why can over-dispersion matter generally?

In general, over-dispersion means that observed variability exceeds what a statistical model assumes. When it occurs, standard errors can be too small if the extra variation is ignored, which can make confidence intervals too narrow and statistical evidence appear stronger than warranted. This is a general consideration in statistical modeling, not a finding about this trial. The registry record does not report an over-dispersion assessment for the primary endpoint.

How do the secondary methods differ?

Progression-free survival is also a time-to-event endpoint, but it concerns progression or death according to its outcome definition, and the posted result uses investigator assessment. Tumors were assessed at 8 week intervals. The registry reports a log-rank hazard ratio for this outcome as well. By contrast, objective tumor response and disease control are reported as percentages of participants, and sponsor analyses use the Cochran-Mantel-Haenszel method. That method is a stratified comparison of categorical outcomes; its reported difference need not have the same numerical sign convention as a simple difference calculated directly from the displayed percentages.

Different outcome types call for different estimates and tests. A hazard ratio summarizes time-to-event comparisons, whereas a risk difference summarizes a contrast in proportions. The analysis method, outcome definition, and contrast direction must be checked before interpreting a sign or magnitude. The registry record does not state all stratification factors, detailed model specifications, or missing-data procedures for the secondary analyses.

For the binary secondary outcomes, simple unadjusted recalculations are available from the posted summaries, alongside sponsor analyses. They are not replacements for the sponsor’s analyses, which may use stratification or other features not represented by the summary calculations. No discrepancy is flagged in the registry entries, but the methods target different analytic constructions. The primary time-to-event interpretation remains based on the sponsor-reported hazard ratio.

11. Confidence Intervals and Precision

The primary median estimates have 95% confidence intervals: 178.0 to 222.0 days for regorafenib plus best supportive care and 134.0 to 177.0 days for placebo plus best supportive care. These intervals communicate uncertainty in each group’s median estimate. They do not directly provide a confidence interval for the difference between the medians, and overlap or non-overlap between separate intervals is not a substitute for the reported between-group test.

For the primary hazard ratio, the estimate is 0.774 and its 95% confidence interval is 0.636 to 0.942. The interval gives a range of relative hazard values compatible with the analysis at the stated confidence level. Its position below 1 is consistent with the direction of the reported comparison. The interval’s width indicates that the estimate is not exact; a range of effect sizes remains compatible with the data and method. Precision is different from importance: a narrow interval can still surround an effect whose practical meaning requires clinical context, while a statistically notable result does not by itself establish a particular benefit for every person.

Confidence intervals reflect sampling uncertainty under the analysis and assumptions. They do not automatically account for incomplete follow-up, systematic differences in care, measurement limitations, unreported analytic choices, or the consequences of examining multiple outcomes. The record does not provide enough detail to evaluate all of those sources of uncertainty. The reported precision should therefore be understood as conditional on the analysis used rather than as a complete measure of uncertainty about the clinical question.

Secondary intervals vary by outcome and estimand. A confidence interval for a hazard ratio is on a relative time-to-event scale, while intervals for differences in proportions are on an absolute percentage-point scale when expressed that way. These should not be compared as if they were the same quantity. The registry’s listed endpoint-specific estimates and intervals are best interpreted within their own outcome definitions and methods.

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 illustrations describe hypothetical future study sizes based on the observed effect, not the original trial’s design justification. The original design assumptions and sample-size rationale are not reported in the registry record. For time-to-event outcomes, the entries are total event counts needed for the stated power targets, not participants per arm. For the other outcomes, entries are participants per arm.

The calculations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the stated fraction of the observed effect as the effect to detect. The rows labelled as planning for 100%, 75%, or 50% of the observed effect therefore represent different hypothetical effect sizes. Smaller effects require more information to distinguish from the null under the same assumptions, so the corresponding illustrations require more events or participants.

The 80% power column means that, under the planning assumptions and specified effect, a study of the indicated size would have an 80% chance of rejecting the null hypothesis if that effect were the true effect. The 90% column describes the corresponding chance at the larger power target. Power is a design property for a specified assumed effect and analysis; it is not a probability that the observed finding is true.

These figures are planning illustrations, not observed power for the completed study. They should not be read as evidence that the trial was designed for a particular effect, because its own original assumptions are not reported in the registry record. The curve and related planning entries are useful for understanding how required information changes when the target effect or power target changes, but they do not replace a protocol-based sample-size calculation.

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 = 0.774, so ln(HR) = -0.2562.
2. d = 4 × (1.96 + 0.842)² / [ln(0.774)]² = 478.4, rounded up to 479 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 <- 0.774                              # 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(1103323)
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 = 479 (80% power), 641 (90% power)
 75% of observed effect: events = 851 (80% power), 1,139 (90% power)
 50% of observed effect: events = 1,914 (80% power), 2,562 (90% power)
Simulated power with 479 events: 0.806 (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 703 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 760 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 <- 4.96438356164384          # control-arm median, months (converted from the posted unit)
hr          <- 0.774          # 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: 422         p (1-sided)   0.0001
 Events: 216        ~HR at bound   0.6034
   Month: 14    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.77   0.0338
   IA 2: 67%                   Z   2.5114
      N: 678         p (1-sided)   0.0060
 Events: 432        ~HR at bound   0.7852
   Month: 23    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.77   0.5603
       Final                   Z   1.9930
      N: 704         p (1-sided)   0.0231
 Events: 648        ~HR at bound   0.8550
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.77   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-reported primary analysis gives a hazard ratio of 0.774, a 95% confidence interval of 0.636 to 0.942, and p = 0.005 using the log-rank method. These are the primary between-group time-to-event results to use in interpreting the registry record. The record does not flag a discrepancy between the sponsor result and the available recalculations.

A hazard ratio cannot be reconstructed from the two reported median survival estimates alone. The posted time-to-event interpretation therefore uses the sponsor’s analysis rather than treating an unadjusted calculation from summary statistics as an equivalent result. The sponsor’s analysis takes precedence if a discrepancy is recorded; no such discrepancy is indicated in the registry entries.

For the categorical secondary outcomes, the sponsor used Cochran-Mantel-Haenszel analyses, while the simple recalculations use posted counts and proportions without the same stratified method. As a result, their estimates can differ in method and contrast coding, and they should not be substituted for one another. The sponsor’s analyses are the official reported tests; the recalculations are useful as straightforward summaries of the posted group data, not as a correction or replacement of the sponsor’s results.

16. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is identified as intent to treat. In general, an intent-to-treat analysis compares participants according to randomized assignment, which preserves the purpose of randomization even when treatment exposure changes. The registry labels the primary population this way, but does not provide a detailed accounting of exclusions, treatment discontinuations, or the handling of every participant’s endpoint data.

The primary outcome description specifies censoring for participants alive at analysis and for those lost to follow-up without contact after randomization. It does not report the amount of missing follow-up, reasons for loss, or sensitivity analyses that test alternative assumptions about missing outcomes. The full missing-data procedures for secondary outcomes are also not reported in the registry record. This limits assessment of whether incomplete observation could affect estimates.

The timeframe states that the database cut-off was used for the 2nd planned formal interim analysis. This identifies the analysis context recorded for the outcome, but does not provide the complete interim monitoring plan, the number or timing of all planned looks, or any alpha-spending approach. Those details are not reported in the registry record and should not be inferred from the phrase describing the cut-off.

The record lists multiple secondary outcomes and analyses but does not report a strategy for controlling multiplicity, such as a prespecified sequence, adjustment method, or allocation of type I error. Without that information, secondary p-values do not have a clearly documented family-wise interpretation in the registry entry. This does not erase the descriptive results, but it means their inferential strength should be treated as more limited than that of a prespecified primary comparison.

Other protocol and analysis details, including the original sample-size justification and a full statistical analysis plan, are not reported in the registry record. The available entries support interpretation of the estimates as posted, but do not allow a complete audit of all design choices, analysis decisions, or sensitivity checks.

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: ascites (25.0%), vomiting (25.0%), death not associated with ctcae term, disease progression nos (25.0%), constitutional symptoms - other (9.1%), fever (3.4%).

The registry lists serious adverse event figures for the regorafenib plus best supportive care group, the placebo plus best supportive care group, and a separate group labelled placebo - regorafenib after unblinding. For the first two groups, 500 and 253 were at risk for serious events, and 232 and 103 were recorded as affected, respectively. The after-unblinding group lists 4 at risk and 2 affected. These are registry counts, not evidence by themselves that an event was caused by a particular treatment.

The record also lists other adverse-event figures: 500 at risk and 489 affected for regorafenib plus best supportive care; 253 at risk and 229 affected for placebo plus best supportive care; and 4 at risk and 4 affected for the after-unblinding group. Affected participants and participants at risk are different entries, and these categories should not be confused with serious adverse events. Death counts are not reported in the registry record.

Listed serious-event terms include Ascites, Vomiting, Death not associated with CTCAE term, Disease progression NOS, Constitutional symptoms - Other, Fever, and Liver dysfunction, with the percentages recorded for each term. The registry entry does not give the event-level context needed to determine causality, severity patterns beyond the serious-event classification, timing, or comparative risk for each term. The separate after-unblinding group should not be merged with either randomized arm by assumption.

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

The primary result describes a between-group comparison of overall survival in a randomized study of people with metastatic colorectal cancer after standard therapy. The registry reports longer median survival in the regorafenib-plus-best-supportive-care group than in the placebo-plus-best-supportive-care group, alongside a hazard ratio below 1 and a confidence interval below 1. The reported log-rank p-value indicates statistical evidence against the null comparison under the sponsor’s analysis.

This does not mean that every participant in the regorafenib group lived longer than every participant in the placebo group. Group medians do not predict an individual’s survival, and the hazard ratio is a relative summary of event rates over follow-up rather than an individual probability. The results also do not, on their own, establish the size of a clinically important effect or resolve how benefits and harms should be weighed.

The study compared regorafenib plus best supportive care with placebo plus best supportive care. It did not compare regorafenib with no supportive care, and the posted results concern the regimens and population described in the registry. The findings should not be generalized automatically to other populations, earlier disease settings, different treatment schedules, or different care contexts. The record does not report enough information to define those boundaries more precisely.

Statistical evidence is conditional on design, conduct, measurement, follow-up, and analysis. The registry provides a primary analysis and selected secondary and safety results, but does not supply the full protocol, the complete analysis plan, multiplicity procedures, or detailed missing-data sensitivity analyses. The results therefore support reading the posted estimates with their stated uncertainty while recognizing that the public record does not answer every methodological question.

Finally, a statistically significant result is not equivalent to proof of a biological mechanism, certainty about future outcomes, or a recommendation for an individual. The registry data describe the comparison made in the trial. They do not provide medical advice or determine how a treatment should be used in a particular clinical situation.

19. Why This Trial Matters Statistically

This trial is statistically informative because it uses a randomized, masked, placebo-controlled comparison for a primary outcome that measures time to death from any cause. The parallel-group design and intent-to-treat designation provide a framework for comparing assigned strategies, while the survival endpoint uses follow-up information from participants with differing observation times. The registry reports both group medians and a hazard ratio, giving readers complementary summaries rather than a single measure.

The record also illustrates why estimates, uncertainty intervals, and test results should be read together. The hazard ratio is a relative time-to-event summary, whereas the median is an absolute time summary. The 95% confidence intervals communicate uncertainty in the reported estimates, and the log-rank p-value addresses evidence under a null comparison. These quantities answer different questions; none replaces the others.

Secondary outcomes show the importance of separating outcome types and analysis methods. Time-to-event comparisons use hazard ratios, while categorical outcomes use percentages and stratified analyses. Their estimates are not directly interchangeable, and multiple secondary tests raise interpretive questions when the multiplicity plan is not reported. The trial therefore demonstrates why a coherent pattern across outcomes can be useful context without turning secondary findings into independent confirmation.

The safety entries likewise require careful reading. Counts of affected participants and those at risk are distinct, and a registry-listed event term does not establish causation. The separate after-unblinding group and the absence of reported death counts underscore the need to retain the registry’s group labels and limitations rather than infer a complete safety profile from selected entries.

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 does not provide the full protocol or statistical analysis plan. In particular, the original sample-size justification, detailed randomization procedures, full interim monitoring plan, and multiplicity strategy are not reported. The timeframe identifies a cut-off used for the 2nd planned formal interim analysis, but does not describe the complete monitoring process or its effect on inference.

Outcome ascertainment and follow-up details are limited in the posted record. Overall survival censoring rules are specified, but the amount and reasons for loss to follow-up, missingness analyses, and sensitivity checks are not reported. Progression-free survival and tumor outcomes relied on investigator assessment, with tumor assessments at 8 week intervals; the record does not provide further detail on assessment procedures or independent review for these outcomes.

The registry reports medians and a sponsor-reported hazard ratio for overall survival, but does not include enough information to evaluate the hazard pattern over time or reconstruct the survival curves. The outcome-specific arm counts and the overall enrollment entry are both reported, but the record does not explain their relationship. No reconciliation should be inferred.

The safety record contains counts for randomized groups and a separate after-unblinding group, but does not provide enough context to infer causality or a complete comparative safety profile. Death counts are not reported in the registry record. Serious-event terms and percentages are listed, but further details about timing, recurrence, or attribution are absent in the registry record described. These limitations constrain interpretation of the posted results without changing what the registry reports.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Patients With Metastatic Colorectal Cancer Treated With Regorafenib or Placebo After Failure of Standard Therapy — NCT01103323.
• Registry record last updated 2015-06-24; status last verified 2015-05.
• Results first posted 2012-11-19.
• 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 matching placebo plus best supportive care in metastatic colorectal cancer after standard therapy. It lists enrollment of 760, Bayer as sponsor, study start 2010-04, primary completion 2011-07, and completed status.

Overall survival was the primary endpoint in the intent-to-treat population. The registry reports median survival of 196.0 days for regorafenib plus best supportive care and 151.0 days for placebo plus best supportive care, with a sponsor-reported hazard ratio of 0.774 (95% confidence interval 0.636 to 0.942; p = 0.005).

Secondary outcomes include progression-free survival, objective tumor response, disease control, and tumor response. The record also includes adverse-event counts and serious-event terms. Details about multiplicity, the original sample-size rationale, full interim procedures, and several missing-data and safety questions are not reported in the registry record.