A Study Comparing the Efficacy and Safety of Vanucizumab and FOLFOX With Bevacizumab and FOLFOX in Participants With Untreated Metastatic Colorectal Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Comparing the Efficacy and Safety of Vanucizumab and FOLFOX With Bevacizumab and FOLFOX in Participants With Untreated Metastatic Colorectal Cancer (NCT02141295), a randomized phase 2 study. The primary outcome is Progression-free Survival (PFS), Time to Event.

2. Clinical Question

This is a comparison of two treatment strategies, each combining an antibody with the same chemotherapy backbone. The primary endpoint focuses on the time until progression or death rather than on a single tumor assessment. That makes the question about the course of disease during follow-up, using events recorded over time. The registry record does not report the rationale for choosing this endpoint or the original sample-size justification.

3. Trial Design

The trial was a Phase II, multicenter, randomized, double-blind, parallel-group study. It had two parts: an open-label, single-arm safety run-in and a randomized comparison. The run-in was intended to confirm the dose and schedule for vanucizumab used in the randomized part. The registry summary says at least 6 eligible participants were to receive vanucizumab with mFOLFOX-6 during the run-in; the safety group in the posted adverse-event results contains 8 participants.

In Part 2, participants were allocated in a 1:1 ratio to vanucizumab plus mFOLFOX-6 or bevacizumab plus mFOLFOX-6. The primary endpoint results include 94 participants in the vanucizumab group and 95 in the bevacizumab group. The registry reports total enrollment of 197. It does not explain how total enrollment relates to the analysis populations or give a detailed disposition of participants across the two parts.

Both treatment groups received induction therapy with mFOLFOX-6 and their assigned antibody. The summary describes up to 8 induction cycles. Maintenance treatment consisted of the assigned antibody with 5-fluorouracil and folinic acid, planned for up to 24 months or until disease progression, unacceptable toxicity, investigator decision, or consent withdrawal. Treatment was given on Day 1 of each 14-day cycle according to the registry summary.

The registry lists the study as terminated. Its recorded start date is 2014-06-30, and the primary completion date is 2016-07-29. The reason for termination, the date on which the study was terminated, and any consequences for follow-up are not reported in the registry record. Further operational details, including the randomization procedure, concealment process, and how masking was maintained, are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Participants with previously untreated metastatic colorectal cancer (mCRC) as defined by RECIST v1.1 were enrolled globally from 7 countries.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: This analysis was based on the ITT population, which consisted of all participants who were randomized (Part II only) and received any amount of the study treatment (5 FU/folinic acid, oxaliplatin, bevacizumab, or vanucizumab) in the bevacizumab + mFOLFOX-6 and vanucizumab + mFOLFOX-6 arms. Participants in the safety-run in were not included.

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 (PFS), Time to Event, measured over Baseline, every 8 weeks, up to approximately 29 months.

Progression-free survival (PFS) is a time-to-event endpoint. In this trial it was defined as the time from randomization to the first documented disease progression or death from any cause on study, whichever occurred first. Death on study was defined as death from any cause within 30 days of the last study treatment. The registry describes assessments at baseline and every 8 weeks, with follow-up extending up to approximately 29 months.

The median PFS is the time by which half of the participants in the analysis population have experienced the defined event, subject to the methods used to account for participants who have not yet had an event. The median gives a compact description of the event-time distribution, but it does not describe every point in the follow-up period. A hazard ratio compares the event rates over time between groups under the model used; it is not a ratio of the two medians.

General: PFS is often used in cancer trials because it combines documented progression and death into an outcome that can occur before overall survival is fully observed. It can therefore describe disease control over the period covered by follow-up. Interpretation depends on how progression is assessed, how censoring is handled, and whether the analysis assumptions are appropriate. The registry identifies investigator assessment using RECIST v1.1, but further detail about assessment procedures, censoring rules, and missing or unevaluable assessments is not reported in the registry record.

7. Results Posted in the Registry

• Vanucizumab + mFOLFOX-6 vs Bevacizumab + mFOLFOX-6: hazard ratio 0.91 (95% CI 0.60–1.39), reported p = = 0.6753 (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 (OS)

• 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:
  • Vanucizumab + mFOLFOX-6 vs Bevacizumab + mFOLFOX-6: hazard ratio 0.85 (95% CI 0.49–1.49), reported p = = 0.5740 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Vanucizumab + mFOLFOX-6 vs Bevacizumab + mFOLFOX-6 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering objective response, duration of objective response, overall survival, adverse events, human anti-human antibodies against vanucizumab, and vanucizumab exposure measures. Detailed numerical results are not reported in the registry record for all listed secondary outcomes. Overall survival has a posted comparison, but the other listed secondary endpoint estimates are not available in the record used for this interpretation.

The overall-survival comparison has the same broad inferential pattern as the primary PFS analysis: the reported hazard-ratio confidence interval includes 1, and the result does not establish a clear difference between treatment groups. This consistency in the direction of uncertainty does not turn the secondary endpoint into confirmation of the primary result. The endpoints measure different aspects of outcome and are observed over different follow-up periods.

Secondary outcomes can help describe the broader pattern of efficacy, safety, and drug exposure, but they usually carry less inferential weight than a prespecified primary endpoint. When multiple outcomes are examined, the chance of at least one apparently notable result can increase, particularly if no adjustment or hierarchy controls the overall error rate. The registry record does not report a multiplicity adjustment, testing hierarchy, or a plan describing which secondary outcomes were confirmatory. Results for secondary outcomes should therefore be treated as supportive or exploratory unless their prespecified status and multiplicity handling are documented.

The record lists 13 posted secondary outcomes. It does not report the analysis population, missing-data approach, or complete statistical results for each of them. Without those details, a comprehensive assessment across the secondary outcomes is not possible. Their presence broadens the range of questions the study addressed, but it does not alter the interpretation of the PFS estimate or resolve its uncertainty.

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

• Percentage of Participants With Objective Response (ORR) as Assessed Using RECIST v. 1.1
• Duration of Objective Response, as Assessed Using RECIST v. 1.1
• Overall Survival (OS)
• Percentage of Participants With Adverse Events (AEs)
• Number of Participants With Human Anti-human Antibodies (HAHAs) Against Vanucizumab
• Area Under the Plasma Concentration-Time Curve (AUC) of Vanucizumab
• Maximum Observed Plasma Concentration (Cmax) of Vanucizumab
• Minimum Observed Plasma Concentration (Clast) of Vanucizumab

9. Statistical Interpretation

10. Statistical Methods Explained

General: A time-to-event analysis follows participants from a defined starting point until an event occurs or follow-up ends. For the primary endpoint, the starting point was randomization and the event was the first documented progression or death from any cause on study. Participants whose event was not observed during their available follow-up may be censored. Censoring allows their observed follow-up to contribute information up to the point at which they leave observation, but valid interpretation depends on assumptions about why follow-up ends. The registry does not report the censoring rules or the number of censored participants.

What the median describes

The median is a summary of the estimated event-time distribution: it marks the point by which half of the population is estimated to have had the event. It is not an average, and it does not indicate that every participant experienced an event at that time. The PFS medians were 338.0 days and 309.0 days in the vanucizumab and bevacizumab groups, respectively. A median can be helpful for describing a group, but comparing two medians does not use all the information in the event-time data in the same way as a time-to-event model.

How to read the hazard ratio

The primary comparison used a Cox regression model and reported a hazard ratio. General: the hazard is the instantaneous event rate among participants who remain at risk at a given time. A hazard ratio compares those rates between groups over follow-up, subject to the model and its assumptions. A value of 1 corresponds to equal hazards under that comparison; a value below 1 points toward a lower estimated hazard in the first-named group, and a value above 1 points toward a higher estimated hazard. This direction describes the estimate, not a causal conclusion by itself.

The reported PFS hazard ratio was 0.91. Its 95% confidence interval was 0.60 to 1.39. Because the interval includes 1, the data are compatible with no difference in the modeled hazards as well as with effects in either direction. The registry reports p = 0.675 for this comparison. A p-value measures how unusual data at least as incompatible with a specified null model would be if that null model and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect.

The Cox model is commonly interpreted under a proportional-hazards assumption: the hazard ratio is treated as sufficiently stable over time. If the relative hazards change over follow-up, a single hazard ratio may not capture the pattern well. The registry does not report a test or graphical assessment of proportional hazards, details of covariate adjustment, or the specific model diagnostics. These omissions do not establish that the assumptions failed; they mean that the record does not allow their assessment.

Why an interval matters

General: a confidence interval expresses uncertainty around an estimate under the statistical model. A 95% confidence interval is produced by a procedure that, under its assumptions and repeated use, would cover the underlying parameter in 95% of such intervals. It is not a statement that there is a 95% probability that this particular interval contains the parameter. A wider interval indicates less precision than a narrower interval, all else being equal. The primary interval spans values below and above 1, so the point estimate should not be interpreted in isolation.

The overall-survival analysis used a log-rank method and reported a hazard ratio of 0.85 with a 95% confidence interval from 0.49 to 1.49 and p = 0.574. The registry identifies the method as Log Rank. It does not report enough detail to determine all the model or estimation procedures underlying the reported hazard ratio. As with the primary analysis, the interval includes 1 and leaves uncertainty about the direction and size of the comparative effect.

Over-dispersion and model fit

General: over-dispersion describes more variability in data than a statistical model assumes. It is especially relevant to count outcomes, where an overly restrictive variance assumption can make uncertainty appear smaller than it is. The primary and overall-survival endpoints are time-to-event outcomes, so count-model over-dispersion is not the central issue for the reported hazard ratios. Model fit and the proportional-hazards assumption are more directly relevant. The registry does not report diagnostics that would establish whether those assumptions were checked or met.

The posted estimates should therefore be interpreted as the sponsor’s reported statistical analyses, with uncertainty judged from the reported confidence intervals and the limitations of the registry’s methodological detail. No recalculated hazard ratio is presented in the record. The analysis population description and the absence of detailed information about censoring, model specification, and diagnostics remain important when judging how robustly the estimates represent the randomized comparison.

11. Confidence Intervals and Precision

The PFS hazard ratio estimate is 0.91, with a 95% confidence interval from 0.60 to 1.39. The interval includes 1, the value corresponding to equal hazards in the comparison, and permits estimates on either side of that value. It therefore does not support a precise claim about the direction of the difference. The interval is the main guide to uncertainty around the hazard-ratio estimate; the point estimate alone would give an incomplete account.

The PFS medians are reported with 95% confidence intervals: 312.0 to 381.0 days for vanucizumab and 284.0 to 352.0 days for bevacizumab. These intervals describe uncertainty in each median estimate. They are not the confidence interval for the difference between medians, and their overlap or separation should not be used as a substitute for the reported comparison analysis.

For overall survival, the reported hazard ratio is 0.85, with a 95% confidence interval from 0.49 to 1.49. That interval also includes 1 and is consistent with a range of comparative effects. The vanucizumab median is 746.0 days, with a lower confidence limit of 687.0 days; its upper confidence limit is not reported in the registry record. The bevacizumab median and the upper confidence limits for the medians are not reported in the registry record.

General: confidence intervals are estimates of precision conditional on the analysis model, data, and assumptions. They do not account for every possible source of uncertainty, such as biases from missing data, outcome assessment, or analysis choices. Since the registry does not give details of censoring, missing-data handling, model diagnostics, or the original sample-size rationale, the intervals should be read as statistical uncertainty within the reported analyses rather than as a complete measure of all uncertainty about the trial.

12. Planning a Similar Trial: Sample Size

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

The event-count planning figures for PFS and overall survival are total events, not participants per arm. They are planning illustrations based on the observed effect, using a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The registry’s original sample-size assumptions and justification are not reported in the registry record. These figures are not observed power.

For PFS, planning for 100% of the observed effect corresponds to 3,530 total events for 80% power and 4,726 total events for 90% power. Planning for 75% of the observed effect corresponds to 6,276 total events for 80% power and 8,401 total events for 90% power. Planning for 50% of the observed effect corresponds to 14,120 total events for 80% power and 18,902 total events for 90% power.

For overall survival, planning for 100% of the observed effect corresponds to 1,189 total events for 80% power and 1,592 total events for 90% power. Planning for 75% of the observed effect corresponds to 2,114 total events for 80% power and 2,829 total events for 90% power. Planning for 50% of the observed effect corresponds to 4,755 total events for 80% power and 6,366 total events for 90% power.

In plain terms, the 80% power column describes the event count used in the illustration to give an 80% chance of detecting the specified effect under its assumptions if that effect is real. The 90% power column uses a higher chance of detection for that same specified effect. Detecting a smaller effect generally requires more information, which in these time-to-event illustrations means more total events. The curve should be read in the same planning context: it displays the relationship between the assumed effect and the required event count, not the chance that this completed trial found a real effect.

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 = 0.910, so ln(HR) = -0.0943.
2. d = 4 × (1.96 + 0.842)² / [ln(0.910)]² = 3,529.8, rounded up to 3,530 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 <- 0.91                              # 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(2141295)
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 = 3,530 (80% power), 4,726 (90% power)
 75% of observed effect: events = 6,276 (80% power), 8,401 (90% power)
 50% of observed effect: events = 14,120 (80% power), 18,902 (90% power)
Simulated power with 3,530 events: 0.794 (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 5,693 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 197 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 <- 10.158904109589          # control-arm median, months (converted from the posted unit)
hr          <- 0.91          # 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: 4148         p (1-sided)   0.0001
 Events: 1594        ~HR at bound   0.8304
    Month: 17    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.91   0.0338
    IA 2: 67%                   Z   2.5114
      N: 5694         p (1-sided)   0.0060
 Events: 3187        ~HR at bound   0.9149
    Month: 28    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.91   0.5603
        Final                   Z   1.9930
      N: 5694         p (1-sided)   0.0231
 Events: 4780        ~HR at bound   0.9440
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.91   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 posted PFS comparison reports a Cox regression hazard ratio of 0.91, a 95% confidence interval from 0.60 to 1.39, and p = 0.675. The overall-survival comparison reports a hazard ratio of 0.85, a 95% confidence interval from 0.49 to 1.49, and p = 0.574. These are the sponsor’s reported analyses in the registry record. The record does not flag a discrepancy between a sponsor analysis and a recalculation, so the reported comparisons are the basis for interpretation.

The planning illustrations are separate from those reported treatment comparisons. They use observed effects as inputs for hypothetical planning scenarios and do not replace the sponsor’s endpoint analysis. Their assumptions include a two-sided significance level of 0.05, equal allocation, and a normal approximation. The original trial-design assumptions are not reported in the registry record, so the illustrations should not be taken as evidence of what the sponsor planned before the trial began.

For the primary and secondary time-to-event comparisons, the reported confidence intervals include 1. The reported p-values are not small, and the estimates should be interpreted with their uncertainty rather than as proof of a treatment difference or proof of equivalence. The registry does not report a fuller statistical analysis plan, including all model specifications and planned sensitivity analyses, so the relationship between the posted analyses and any prespecified analysis plan cannot be fully evaluated.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study tests or estimates multiple outcomes, subgroups, time points, or other comparisons. If many hypotheses are assessed without an appropriate plan, the chance of at least one nominally significant result can increase. This does not mean every multiple-outcome analysis is invalid; it means the analysis plan should clarify which endpoint is primary, how secondary outcomes are ordered, and whether inferential adjustments are used.

The registry identifies PFS as the primary endpoint and lists 13 secondary outcomes. It does not report whether a multiplicity correction was planned, whether secondary endpoints were arranged in a testing hierarchy, or whether any secondary findings were intended to be confirmatory. The reported p-values should therefore be interpreted as endpoint-specific results, not as evidence that the overall family of outcomes was controlled for multiplicity.

Missing-data handling and censoring are also important for time-to-event outcomes. A participant with no recorded event may contribute follow-up until the last known assessment, after which the observation may be censored. Inference can be affected if reasons for ending observation are related to the likelihood of an event. The registry defines PFS and names the analysis population, but detailed censoring rules, methods for handling missing assessments, and sensitivity analyses are not reported in the registry record.

The primary analysis population is described as randomized Part 2 participants who received any amount of study treatment. The registry does not report whether results were also analyzed in all randomized participants without that treatment condition, or how many randomized participants were excluded from the stated analysis population. It also does not report detailed participant flow or reasons for exclusions. These gaps limit assessment of how closely the analysis followed the randomized groups.

Interim analyses and stopping boundaries are not reported in the registry record. The reason for the terminated status is also not reported. Without those details, it is not possible to assess whether any early review or study discontinuation affected the amount or interpretation of follow-up. These are limits in the available record, not evidence that a particular analysis or procedure was or was not performed.

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: neutropenia (12.5%), cardiac failure (12.5%), intestinal obstruction (12.5%), nausea (12.5%), vomiting (12.5%).

The posted safety figures distinguish the safety run-in from the two randomized treatment groups. Serious adverse events affected 3 of 8 participants in the safety run-in, 46 of 93 participants receiving vanucizumab plus mFOLFOX-6, and 41 of 95 participants receiving bevacizumab plus mFOLFOX-6. Other adverse events were reported for 8 of 8, 91 of 93, and 94 of 95 participants in those respective groups. These are participant counts in the registry’s safety summaries, not comparative estimates adjusted for follow-up or other factors.

The registry lists neutropenia, cardiac failure, intestinal obstruction, nausea, and vomiting at 12.5% each among the top serious adverse-event terms, and febrile neutropenia at 5.3%. The record does not provide enough context in these summaries to infer comparative risk from these terms alone. Serious adverse-event categories and event terms should not be interpreted as proof that treatment caused an event.

Deaths are recorded for 3 participants in the safety run-in, 24 in the vanucizumab group, and 27 in the bevacizumab group. These counts alone do not specify cause, timing, relation to treatment, or exposure-adjusted risk. The registry’s summarized safety information is useful for describing reported events, but a complete comparative safety assessment would require fuller event definitions, follow-up details, and causal assessment information.

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

The results describe what was observed in the registry’s reported analyses: the PFS medians were 338.0 days and 309.0 days, and the reported hazard ratio was 0.91. Its 95% confidence interval, 0.60 to 1.39, includes 1. The overall-survival hazard ratio was 0.85, with a 95% confidence interval from 0.49 to 1.49. Neither comparison gives a precise estimate that rules out no difference under the reported analysis.

These data do not establish that vanucizumab plus mFOLFOX-6 is superior to bevacizumab plus mFOLFOX-6. They also do not establish that the regimens are equivalent or that a meaningful difference has been excluded. A non-significant result can reflect a small or absent difference, or limited precision; the confidence interval is needed to understand which effect sizes remain compatible with the data. The registry does not report a prespecified equivalence or non-inferiority margin.

The findings apply to the studied comparison and the analysis populations described in the registry. The trial included a safety run-in and a randomized Part 2, while the PFS analysis population is described as randomized participants who received any amount of study treatment. The record does not give enough detail to evaluate all exclusions, missing observations, or sensitivity analyses. It also does not report the reason for termination, so the effect of termination on follow-up cannot be determined from this record.

General: a clinical-trial estimate is not a guarantee of an individual outcome, and a statistical comparison is not a treatment recommendation. The interpretation is limited to the reported endpoint estimates and their uncertainty. It does not provide medical advice or establish how the findings should guide care.

19. Why This Trial Matters Statistically

This trial is statistically informative because it compared two antibody-plus-chemotherapy strategies in a randomized, double-blind Phase II design and reported time-to-event outcomes. Randomization supports a structured comparison between treatment groups, while blinding can reduce some forms of bias in treatment administration and outcome assessment. The registry does not describe the procedures used to implement randomization or masking, so those features cannot be evaluated in detail.

The primary result illustrates why effect estimates, confidence intervals, and p-values need to be read together. The PFS point estimate is below 1, but its interval crosses 1 and its reported p-value is 0.675. The estimate does not provide a statistically clear difference, while the interval also does not rule out effects on either side of no difference. A point estimate by itself would conceal that uncertainty.

The planning illustrations also show a general feature of time-to-event study design: the amount of information required depends on the effect targeted. Scenarios targeting smaller fractions of the observed effect require more total events than scenarios using the full observed effect. Those calculations are planning illustrations, not the original design justification, and the registry does not report the assumptions used to plan the actual trial.

Finally, the record places efficacy estimates alongside safety outcomes and secondary measures, but does not provide complete analysis details for every outcome. That makes the trial a useful example of how registry results can support descriptive interpretation while leaving important questions about multiplicity, missing data, model assumptions, and study termination unresolved.

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 reported for this trial. First, the registry lists the study as terminated but does not report why it was terminated or whether termination changed planned follow-up. The recorded primary completion date is 2016-07-29, but the relationship between that date and the termination is not explained.

Second, the primary analysis population is described as randomized Part 2 participants who received any amount of study treatment. The record does not provide a participant-flow account that would show how many randomized participants were excluded from this analysis or why. It also does not report a separate analysis of all randomized participants regardless of treatment received.

Third, methodological detail is limited. The record does not report censoring rules, handling of missing assessments, covariate adjustment for the Cox model, diagnostics for the proportional-hazards assumption, or sensitivity analyses. It also does not report the original sample-size justification, planned interim analyses, or full multiplicity procedures. These gaps make it difficult to assess the robustness and prespecification of the reported results.

Fourth, detailed results are not reported in the registry record for all listed secondary endpoints. The overall-survival median for the bevacizumab group and some confidence limits are also not reported. The safety summaries give participant counts and selected serious adverse-event terms, but do not provide enough detail to determine event timing, exposure-adjusted rates, or treatment attribution from those figures alone.

These limitations concern what can be concluded from the registry record. They should not be taken as evidence that unreported procedures were not conducted or that the reported analyses are incorrect.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study Comparing the Efficacy and Safety of Vanucizumab and FOLFOX With Bevacizumab and FOLFOX in Participants With Untreated Metastatic Colorectal Cancer — NCT02141295.
• Registry record last updated 2020-03-25; status last verified 2020-03.
• Results first posted 2020-03-25.
• 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

NCT02141295 is a terminated Phase II, multicenter, randomized, double-blind, parallel-group study sponsored by Hoffmann-La Roche. It compared vanucizumab plus mFOLFOX-6 with bevacizumab plus mFOLFOX-6 in participants with previously untreated metastatic colorectal cancer. The registry reports enrollment of 197 and describes an open-label safety run-in followed by a randomized comparison.

The primary endpoint was investigator-assessed PFS using RECIST v1.1. The reported PFS hazard ratio was 0.91, with a 95% confidence interval from 0.60 to 1.39 and p = 0.675. The overall-survival hazard ratio was 0.85, with a 95% confidence interval from 0.49 to 1.49 and p = 0.574. Both intervals include 1, leaving uncertainty about the comparative effects.

The registry does not report the reason for termination, the original sample-size rationale, or several details needed to assess missing data, multiplicity, and model assumptions. The posted estimates therefore describe the reported analyses but do not establish superiority, equivalence, or the absence of a meaningful difference.