Nintedanib (BIBF 1120) vs Placebo in Refractory Metastatic Colorectal Cancer (LUME-Colon 1): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nintedanib (BIBF 1120) vs Placebo in Refractory Metastatic Colorectal Cancer (LUME-Colon 1) (NCT02149108), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS) by Central Review Assessment.

2. Clinical Question

The central statistical question is a comparison of time-to-event outcomes, not simply a comparison of whether progression occurred at some point. The registry reports median progression-free survival for each arm and a hazard ratio from a log-rank analysis. These summaries address related but distinct aspects of the observed event-time data: the medians describe the estimated time by which half of the relevant event-time distribution has occurred, while the hazard ratio summarizes a relative event-rate comparison over follow-up under the analysis used.

The question is specific to this trial’s population and treatment context: metastatic colorectal cancer refractory to standard therapies, with both groups receiving best supportive care. It does not directly answer questions about other patient groups, other treatment settings, or comparisons that were not randomized in this study.

3. Trial Design

LUME-Colon 1 was a Phase III, randomized, double-blind, parallel-group study. It compared nintedanib plus best supportive care with placebo plus best supportive care in patients with metastatic colorectal cancer refractory to standard therapies. The registry lists an enrollment of 768 and marks the study as completed. The arm-level primary analysis counts were 382 for placebo and 386 for nintedanib.

Random allocation is intended to create groups that are comparable, on average, at the start of a trial. Blinding is intended to limit the influence of knowledge about treatment assignment on aspects of trial conduct and assessment. The registry identifies the study as double-blind but does not report further details about who was blinded or how blinding was maintained. It also does not report the randomization procedure or allocation-concealment details.

Progression-free survival was assessed by central review. The record defines the endpoint using progression under RECIST version 1.1 or death from any cause, whichever came first. The primary analysis used the Randomised Set: all patients randomized to receive treatment, whether treated or not. The record describes arm-specific medians and confidence intervals from unadjusted Kaplan-Meier curves, and a reported hazard ratio from a log-rank analysis.

The study’s objective was to evaluate nintedanib after failure of previous standard chemotherapy and biological agents. The record names objective tumour response and disease control as secondary outcomes, though detailed results are not posted for every named outcome. The original protocol’s sample-size justification, its planned power assumptions, and further details of the analysis plan are not reported in the registry record. The planning figures shown with the results are illustrations based on the observed effect, not evidence of the assumptions used to design the original trial.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomised Set: This patient set included all patients who were randomised to receive treatment, whether treated or not.

5. Baseline Characteristics

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

Population: Randomised Set (RS): This patient set included all patients who were randomised to receive treatment, whether treated or not.

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS) by Central Review Assessment, measured over From randomisation until cut-off date 14JUN2016..

Progression-free survival measures the time from randomization until the first of two events: disease progression according to RECIST version 1.1, as assessed by central review, or death from any cause. A participant who experiences either event reaches the endpoint at that time. The registry specifies that follow-up for this outcome runs from randomization until the cut-off date 14JUN2016.

This kind of endpoint is used when the timing of progression or death is of interest. It incorporates both whether an event occurred during follow-up and when it occurred, rather than reducing the result to a simple count of participants with an event. Central review provides a specified assessment source for progression, and the record states that the analysis used an unadjusted Kaplan-Meier curve for each arm.

The median is a time-point summary of the estimated event-time distribution. It does not describe every participant’s experience, and it does not by itself show how the groups compared throughout the entire follow-up period. The hazard ratio offers a different summary by comparing event rates over time under the reported analysis. These measures should therefore be read together, while keeping in mind that their interpretations depend on their definitions and analysis conventions. The registry does not report further details about the handling of censoring, missing endpoint information, or the assessment schedule.

7. Results Posted in the Registry

• Placebo vs Nintedanib: hazard ratio 0.58 (95% CI 0.49–0.69), reported p < 0.001 (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.

Disease Control (Complete Response + Partial Response + Stable Disease) by Central Review Assessment

• 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:
  • Nintedanib: 25.6% (99/386) versus 10.5% (40/382) on control; risk difference 15.2 percentage points (95% CI 9.8 to 20.5), risk ratio 2.45 (1.75–3.44); 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 Nintedanib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry names objective tumour response and disease control as secondary outcomes assessed by central review. A detailed numerical disease-control result is posted, while the objective-response result is not reported in the registry record. Across the results that are numerically available, the disease-control pattern is in the same broad direction as the primary arm-median pattern. That directional consistency is descriptive; it does not make the secondary endpoint equivalent to progression-free survival or provide a second test of the same hypothesis.

These outcomes differ in what they measure. Disease control combines complete response, partial response, and stable disease into a status-based outcome. Progression-free survival measures time until progression or death. A participant’s disease-control classification at an assessment and the timing of progression or death are therefore distinct features of the clinical course. The secondary finding can provide context for the primary endpoint, but it cannot explain the primary result or establish a mechanism for it.

The registry reports a sponsor logistic-regression odds ratio for disease control and an unadjusted comparison based on summary counts. These analyses should be kept distinct because the model-based estimate and the unadjusted estimate need not target precisely the same comparison. The record does not include enough model details to evaluate the logistic regression specification fully.

Secondary results generally warrant more caution than a prespecified primary analysis, particularly when several outcomes or comparisons may be examined. Testing multiple outcomes can increase the chance of apparently notable results arising by chance if no multiplicity strategy is used. The registry does not report whether or how multiplicity was controlled. The posted p-values for secondary outcomes should therefore be read as unadjusted unless the record states otherwise; no such adjustment is described. The results are useful as supporting context, but the missing objective-response result and the absence of a reported multiplicity plan limit claims about a consistent secondary-outcome pattern.

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

• Objective Tumour Response (Complete Response (CR)) + Partial Response (PR) by Central Review Assessment
• Disease Control (Complete Response + Partial Response + Stable Disease) by Central Review Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. Its event is the first occurrence of centrally assessed disease progression under RECIST version 1.1 or death from any cause. The reported time begins at randomization. The registry gives an analysis cut-off of 14JUN2016 and identifies the Randomised Set as the analysis population, including randomized patients whether treated or not.

What does the Kaplan-Meier method summarize?

General statistical explanation: Kaplan-Meier estimation uses participants’ observed follow-up times to estimate the proportion who have not yet experienced the event over time. It can account for participants whose event has not been observed by the end of their available follow-up, provided their follow-up is handled as censored. The registry says that an unadjusted Kaplan-Meier curve was used for each arm and that medians and confidence intervals were calculated from those curves. It does not report the detailed censoring rules or the method used to calculate the confidence intervals.

A median from a Kaplan-Meier curve is the estimated time at which the event-free proportion reaches the median point of its estimated distribution. It is a summary of the curve, not an average follow-up time and not an individual prediction. It can be useful because it expresses the time-to-event outcome in the endpoint’s time units. It does not show the whole curve, and two curves can differ in ways that a single median does not capture.

What does the log-rank analysis contribute?

General statistical explanation: the log-rank test compares event-time experience between groups across follow-up, taking account of the timing of events and the participants still under observation at relevant event times. The registry reports a log-rank method for the hazard ratio and gives p < 0.001. The p-value is evidence about compatibility with a null comparison under the test’s assumptions; it is not the probability that the null hypothesis is true, nor does it quantify the magnitude or importance of an effect.

The hazard ratio is a relative time-to-event summary. General statistical explanation: its interpretation depends on which group’s event rate is in the numerator and which group is the reference. The registry’s comparison label reads “Placebo vs Nintedanib,” but the record does not spell out the ratio orientation. Accordingly, the estimate is best cited with that label and its interval rather than translated into an unambiguous arm-specific rate statement. The registry identifies a 95% confidence interval for the reported hazard ratio.

Why does the endpoint definition matter?

Progression-free survival combines progression and death, counting whichever occurs first. That definition means the analysis is not limited to tumour progression alone. Central review and the stated RECIST version define how progression is assessed for this outcome. Different endpoint definitions can produce different event times and different statistical summaries, so interpretation should remain tied to the registry’s definition rather than treating the result as a general measure of every aspect of disease status.

The record also describes a binary disease-control outcome based on complete response, partial response, or stable disease by central review. A binary outcome classifies participants according to whether the specified status was recorded, rather than analyzing the timing of an event. Its posted arm proportions and a sponsor-reported odds ratio are therefore not the same estimand as the primary time-to-event hazard ratio. General statistical explanation: an odds ratio compares the odds of an outcome between groups; it is not itself a risk difference or a probability.

For that secondary endpoint, the registry includes a sponsor-reported logistic-regression odds ratio and an unadjusted recalculation based on posted summary counts. The latter is a simple unadjusted calculation and does not reproduce a regression model with any adjustments. The sponsor’s analysis and an unadjusted calculation answer related but not necessarily identical statistical questions. The registry does not report the full model specification, covariates, or further details needed to reconstruct the sponsor’s regression analysis.

General statistical explanation: over-dispersion matters when the variability in data is greater than a model’s assumptions allow. If present and not accounted for, uncertainty estimates and tests from an overly restrictive model may be misleading. The posted primary outcome is time-to-event and the listed secondary analysis is logistic regression; the registry record does not identify an over-dispersion assessment or report a model issue of this kind. It should not be assumed that such a problem occurred.

11. Confidence Intervals and Precision

The registry reports 95% confidence intervals for the primary medians and hazard ratio. For placebo, the median is 1.38 months with a 95% confidence interval of 1.38 to 1.41 months. For nintedanib, the median is 1.51 months with a 95% confidence interval of 1.45 to 2.17 months. The reported hazard ratio is 0.58, with a 95% confidence interval of 0.49 to 0.69.

General statistical explanation: a confidence interval expresses uncertainty about an estimated quantity under the statistical method used. It is not a guarantee that the true value lies inside the particular interval, and it is not a range intended to contain individual participants’ event times. Interval width reflects precision in the estimate under the analysis, but should be considered alongside the estimand, analysis assumptions, and available data.

The median confidence intervals differ in width: the posted interval for the nintedanib median extends over a broader range than the placebo interval. This indicates that the median estimates have different reported precision; it does not, by itself, explain why. The record does not report the detailed factors determining interval width, such as the number and timing of events contributing to each estimate or the precise interval method.

The hazard-ratio interval describes uncertainty for a different summary from either arm-specific median. Its interpretation also depends on the ratio orientation, which is not made explicit in the registry’s comparison label. A confidence interval should not be read as a direct statement about clinical importance, nor should the arm-specific median intervals be used as a substitute for the reported between-group analysis. No additional precision estimate for unreported secondary outcomes can be inferred from these primary intervals.

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 original trial’s design calculation. For the time-to-event endpoint, the entries are total events required, not participants per arm. For binary outcomes, the entries are participants per arm. The assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning row targets the stated fraction of the observed effect. The registry does not report the original trial’s sample-size assumptions or justification.

The 80% power column gives the illustrated number of events or participants required under those assumptions for an analysis to have an 80% chance of detecting the specified effect, if that effect and the assumptions hold. The 90% power column gives the corresponding planning target for a 90% chance. These are prospective design concepts, not descriptions of what happened in the completed trial. This is not observed power.

The rows labeled as planning for 100%, 75%, and 50% of the observed effect represent different assumed effect sizes for illustration. The smaller the effect a study is designed to detect, the more events or participants are generally needed to distinguish it from random variation under a chosen design. Thus, planning for a smaller fraction of the observed effect calls for larger sample-size targets in the displayed calculations.

For time-to-event outcomes, reaching a target number of events is not identical to enrolling the same number of participants; participants may have different follow-up and some may not experience the event during observation. The registry’s time-to-event figures are totals of events. The binary-outcome figures are per arm, and should not be mistaken for total enrollment. All figures are illustrative calculations and do not establish the assumptions actually used to plan LUME-Colon 1.

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 = 0.580, so ln(HR) = -0.5447.
2. d = 4 × (1.96 + 0.842)² / [ln(0.580)]² = 105.8, rounded up to 106 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 <- 0.58                              # 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(2149108)
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 = 106 (80% power), 142 (90% power)
 75% of observed effect: events = 189 (80% power), 252 (90% power)
 50% of observed effect: events = 424 (80% power), 567 (90% power)
Simulated power with 106 events: 0.762 (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 148 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 768 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 <- 1.38          # control-arm median, months (converted from the posted unit)
hr          <- 0.58          # 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: 66         p (1-sided)   0.0001
  Events: 48        ~HR at bound   0.3416
   Month: 11    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.58   0.0338
   IA 2: 67%                   Z   2.5114
      N: 116         p (1-sided)   0.0060
  Events: 96        ~HR at bound   0.5980
   Month: 19    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.58   0.5603
       Final                   Z   1.9930
      N: 148         p (1-sided)   0.0231
 Events: 144        ~HR at bound   0.7167
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.58   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 primary time-to-event result is reported as the sponsor’s log-rank analysis: a hazard ratio of 0.58, a 95% confidence interval of 0.49 to 0.69, and p < 0.001. The registry’s primary outcome description also reports arm-specific medians from unadjusted Kaplan-Meier curves. For this endpoint, the posted statistical interpretation uses the sponsor-reported hazard ratio rather than replacing it with an independently recalculated ratio. The comparison label is “Placebo vs Nintedanib”; the record does not explicitly state the numerator and reference convention, so the reported value should remain attached to that label.

For disease control, the registry posts a logistic-regression odds ratio of 2.96, with a 95% confidence interval of 2.00 to 4.47 and p < 0.001. It also includes an unadjusted recalculation from the posted summary counts. That recalculation does not reproduce the sponsor’s regression model and should not be presented as the sponsor’s adjusted estimate. The two results concern the same broad binary outcome but arise from different analyses.

The distinction is important: a sponsor-reported model result and a simple unadjusted calculation can differ because they need not use the same model or assumptions. The registry record does not describe the full regression specification or provide enough detail to reconstruct it. The posted primary sponsor analysis remains the relevant reported comparison for progression-free survival; secondary recalculations are supplementary descriptions, not replacements for the sponsor’s own analysis.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies progression-free survival by central review as the primary outcome and names objective tumour response and disease control as secondary outcomes. It also records multiple analyses and outcome measures. However, it does not report a multiplicity strategy, such as a hierarchy for testing outcomes or an adjustment to account for multiple statistical tests. Without that information, the family of hypotheses intended to support formal claims is not clear from the registry record.

General statistical explanation: when several outcomes or comparisons are tested, the chance of at least one small p-value arising by chance can increase. Procedures for controlling multiplicity can help manage that risk, but they may affect how each individual result should be interpreted. Since a multiplicity method is not reported, the posted secondary p-values should not be assumed to have been adjusted. The record does not establish whether a strategy was prespecified elsewhere.

The registry defines the primary analysis population as the Randomised Set: all patients randomized to receive treatment, whether treated or not. This supports describing the primary results as based on that set. The record does not provide a detailed account of missing data, censoring rules, withdrawals, or how participants with incomplete endpoint information were handled. Those details matter in time-to-event analyses because the observed follow-up and assumptions about censoring contribute to the estimated curves and comparisons.

The primary endpoint description says that medians and confidence intervals came from unadjusted Kaplan-Meier curves, and the reported comparison used a log-rank method. The record does not report further adjustment variables or a full statistical analysis plan. It also does not describe interim analyses, stopping rules, or whether any prespecified subgroup analyses affected interpretation; those details are not reported in the registry record. Their absence should be treated as uncertainty about what was planned, not evidence that a particular procedure was or was not used.

For disease control, the registry gives a sponsor logistic-regression analysis and a separate unadjusted recalculation. The regression model’s full specification is not reported, and the record does not say whether the analysis was part of a multiplicity-controlled testing sequence. Interpretation should consequently distinguish the primary result from secondary findings and avoid treating nominal significance on its own as conclusive evidence across all outcomes.

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: malignant neoplasm progression (7.0%), dyspnoea (3.1%), alanine aminotransferase increased (1.8%), acute kidney injury (1.8%), intestinal obstruction (1.6%).

The registry lists serious adverse event information by arm. In the placebo group, 133 participants were affected among 381 at risk; in the nintedanib group, 149 were affected among 384 at risk. For other adverse events, the corresponding counts are 309 among 381 at risk for placebo and 351 among 384 at risk for nintedanib. These are counts of affected participants and participants at risk as reported, not measures of event duration or severity beyond the serious-versus-other classification.

The most frequently listed serious terms include malignant neoplasm progression at 7.0%, dyspnoea at 3.1%, alanine aminotransferase increased at 1.8%, acute kidney injury at 1.8%, intestinal obstruction at 1.6%, and blood bilirubin increased at 1.6%. These terms describe events recorded in the registry; the percentages should not be interpreted as proof that treatment caused an event. The record does not report deaths in the adverse-event fields.

Safety counts require context, including definitions, observation periods, attribution rules, and whether participants could experience more than one event. The registry excerpt does not provide those details or a full safety-analysis description. These data are therefore descriptive and should not be used alone to compare an individual’s risk or make a treatment decision.

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

The posted primary results describe progression-free survival in a randomized comparison of nintedanib plus best supportive care and placebo plus best supportive care among patients with metastatic colorectal cancer refractory to standard therapies. The registry reports arm-specific Kaplan-Meier medians and a log-rank hazard ratio with its confidence interval and p-value. Those statistics summarize the registered analysis; they do not provide a complete account of every participant’s outcome or every feature of follow-up.

The median estimates are numerically higher for the nintedanib arm, and the registry reports a hazard ratio of 0.58 with p < 0.001. The comparison label is “Placebo vs Nintedanib,” and the ratio orientation is not explicitly defined in the record. The result should therefore be stated as reported, without assigning a direction to the hazard ratio that depends on an unstated numerator convention. The statistical evidence does not, by itself, establish the clinical importance of the result.

A randomized, double-blind design is intended to support a fair comparison between assigned groups, but registry summaries alone do not establish that every possible source of bias or uncertainty was absent. The record does not report full details of randomization, missing-data handling, multiplicity, or the analysis plan. These gaps constrain assessment of the assumptions and robustness of the reported results.

The results do not determine what will happen to a particular patient, address populations beyond the registered study population, or compare nintedanib with treatments other than the registered placebo-plus-best-supportive-care group. The disease-control result is a secondary outcome and objective tumour response is not reported numerically in the registry record. The posted data should be understood as statistical summaries of this trial, not as medical advice or a universal claim about treatment.

19. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters in clinical statistics. Progression-free survival is not merely a count of tumour responses: it combines the timing of centrally assessed progression with death from any cause, whichever occurs first. That definition determines which events contribute to the analysis and what the resulting summaries mean.

The registry also places several statistical summaries side by side: Kaplan-Meier medians, a log-rank hazard ratio, confidence intervals, and a p-value. Each has a different role. Medians describe a point on the estimated event-time distribution; the hazard ratio summarizes a relative comparison across follow-up; confidence intervals express uncertainty; and the p-value addresses compatibility with a null comparison under the test assumptions. Reading them together is more informative than treating any one value as a complete verdict.

The record is also a practical example of why analysis labels and conventions matter. A hazard ratio must be interpreted with its numerator and reference group in view, yet the comparison label does not explicitly settle that orientation. Similarly, a sponsor’s logistic-regression odds ratio for a secondary outcome is not interchangeable with an unadjusted calculation from summary counts. Statistical estimates are meaningful only when the outcome, population, and method are kept attached to them.

Finally, the registry illustrates the limits of public result summaries. Some outcomes are named without numerical results, and important details of multiplicity, missing-data handling, and original sample-size planning are not reported. A careful reader can describe the posted estimates precisely while separating those observations from claims that require information not in the record.

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 available registry record. The primary hazard ratio is labeled “Placebo vs Nintedanib,” but the record does not explicitly define the numerator and reference group. This limits an unambiguous arm-direction interpretation of the ratio. The medians can be described by arm, but they do not resolve that reporting convention.

The outcome cut-off is stated as 14JUN2016. The record does not provide the detailed follow-up distribution, event counts for the primary endpoint, censoring rules, or the assessment schedule. Without those details, the posted medians and hazard ratio cannot be independently reconstructed from participant-level data. The median confidence intervals also differ in reported width, but the registry does not give enough detail to identify the reasons.

The registry names objective tumour response as a secondary outcome but does not report its numerical result. The available disease-control result is not a substitute for that missing outcome. The secondary analysis includes both a sponsor logistic-regression estimate and an unadjusted recalculation; the full regression specification is not reported, so the model-based result cannot be fully assessed from the record alone.

The record does not report the original sample-size justification, multiplicity plan, interim analyses, full statistical analysis plan, or detailed missing-data methods. Planning illustrations based on the observed effects do not fill those gaps. Adverse-event counts are posted, but detailed definitions, attribution, observation periods, and deaths are not reported in the registry record. These limitations do not negate the reported statistics; they define the boundaries of what can be evaluated from the registry information.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Nintedanib (BIBF 1120) vs Placebo in Refractory Metastatic Colorectal Cancer (LUME-Colon 1) — NCT02149108.
• Registry record last updated 2017-07-21; status last verified 2017-06.
• Results first posted 2017-07-21.
• 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

LUME-Colon 1 was a completed Phase III randomized, double-blind, parallel-group study in metastatic colorectal cancer refractory to standard therapies. It compared nintedanib plus best supportive care with placebo plus best supportive care. The primary endpoint was centrally reviewed progression-free survival, defined as time from randomization to RECIST version 1.1 progression or death from any cause, whichever occurred first.

The registry reports arm-specific Kaplan-Meier medians and a log-rank hazard ratio with a 95% confidence interval and p-value. Disease control is reported as a secondary outcome; the numerical objective-response result is not reported in the registry record. The Randomised Set included all randomized patients, whether treated or not. Important details, including the original sample-size assumptions, multiplicity strategy, and full missing-data methods, are not reported in the registry record.