Capecitabine and Bevacizumab With or Without Atezolizumab in Treating Patients With Refractory Metastatic Colorectal Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Capecitabine and Bevacizumab With or Without Atezolizumab in Treating Patients With Refractory Metastatic Colorectal Cancer (NCT02873195), a randomized phase 2 study. The primary outcome is Progression Free Survival (PFS).

2. Clinical Question

3. Trial Design

BACCI was a randomized, double-blind, placebo-controlled, parallel-group phase II trial sponsored by Academic and Community Cancer Research United. The registry lists an enrollment of 133 and a completed status. The study began on 2017-07-07, with primary completion on 2023-03-06. These dates describe the registry record; they do not by themselves establish the follow-up available for every participant.

Participants were allocated to one of two regimens. One group received atezolizumab, bevacizumab, and capecitabine; the other received placebo, bevacizumab, and capecitabine. The common chemotherapy and biologic treatment helps focus the randomized contrast on the addition of atezolizumab. A double-blind, placebo-controlled design is intended to reduce the influence of treatment knowledge on participant experience, clinical management, and outcome assessment. The registry does not report which specific roles were masked or how masking was maintained.

The listed schedule used intravenous atezolizumab or placebo on day 1, intravenous bevacizumab on day 1, and oral capecitabine twice daily on days 1 through 14, with courses every 21 days. Treatment continued in the absence of progression or unacceptable toxicity. The primary outcome was progression-free survival, assessed by RECIST v1.1, with overall survival and objective response among the posted secondary outcomes. Toxicity was also listed among secondary outcomes.

The primary comparison was described as a superiority analysis using an unstratified log-rank test, with the p-value used for decision-making at a one-sided level of 0.10. A Cox proportional hazards model was specified for estimating the hazard ratio and its 95% confidence interval, while Kaplan-Meier methods were specified for median progression-free survival and curves. Other details of the original design, including sample-size justification and any interim analyses, 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.

Overall Study

Reasons for not completing this period:

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

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), measured over From randomization to first documentation of disease progression by RECIST v1.1, or death from any cause, assessed up to 20 months.

Progression-free survival (PFS) is the time from randomization until the first documented disease progression or death from any cause. In this trial, progression was assessed using RECIST v1.1 and defined as a new lesion or an increase by at least 20% in previously involved sites from nadir. The registry gives an assessment period of up to 20 months.

PFS is a time-to-event outcome: it accounts for both when an event occurs and the fact that some participants may not have had an event by the time their follow-up ended. The median PFS is the time at which the estimated proportion remaining alive without progression reaches one half. It is a summary of the estimated event-time distribution, not a measure of how long every participant remained progression-free.

Comparing PFS can be useful when the clinical question concerns delay in progression or death, and when follow-up may differ among participants. The log-rank test compares the event patterns over follow-up, while a hazard ratio summarizes the relative event rate over time under the model used. Neither statistic alone describes every feature of the survival curves. The registry also reports median PFS by arm and a 95% confidence interval for the hazard ratio, so the size of the estimated contrast and its uncertainty can both be considered.

PFS is not the same as overall survival: its event may be documented progression or death, whereas overall survival counts death from any cause. PFS assessment also depends on the timing and quality of disease evaluations. The registry names RECIST v1.1 but does not report further detail about assessment schedules or handling of missing assessments.

7. Results Posted in the Registry

• Atezolizumab, Bevacizumab, Capecitabine vs Placebo, Bevacizumab, Capecitabine: hazard ratio 0.72 (95% CI 0.49–1.07), reported p = 0.051 (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:
  • Atezolizumab, Bevacizumab, Capecitabine vs Placebo, Bevacizumab, Capecitabine: hazard ratio 0.94 (95% CI 0.56–1.56), reported p = 0.400 (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 Atezolizumab, Bevacizumab, Capecitabine vs Placebo, Bevacizumab, Capecitabine and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Atezolizumab, Bevacizumab, Capecitabine: 8.5% (7/82) versus 4.3% (2/46) on control; risk difference 4.2 percentage points (95% CI -4.3 to 12.6), risk ratio 1.96 (0.43–9.06); unadjusted two-proportion z-test p = 0.374.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atezolizumab, Bevacizumab, Capecitabine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add information on survival, tumor response, and toxicity, but they do not replace the primary PFS comparison. Across the posted efficacy outcomes, the uncertainty is substantial: the overall-survival hazard-ratio interval includes 1, and the objective-response comparison is imprecise. This broad pattern does not provide a clearly precise secondary estimate that resolves the uncertainty in the primary result.

Secondary endpoints can help describe whether findings point in a similar direction across different ways of measuring outcomes. PFS reflects progression or death over time, overall survival reflects death over time, and objective response records whether a response occurred. These endpoints are related but not interchangeable: a change in one does not guarantee a corresponding change in another. The registry's secondary outcomes therefore provide context rather than a single combined verdict.

The record lists toxicity as a secondary outcome, but it does not post a comparative test for that outcome in the results summarized for these efficacy analyses. Safety counts should be read as descriptive event information, not as evidence that one regimen caused more or fewer events. The listed adverse-event counts and terms do not by themselves establish causation.

Multiplicity matters because testing multiple secondary outcomes creates more opportunities for apparently unusual results to arise by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary endpoints. Consequently, unadjusted secondary p-values, where reported, carry less weight as confirmatory evidence than a prespecified primary analysis. They can still describe the data, but should be interpreted cautiously and alongside their confidence intervals and the overall trial design.

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

• Overall Survival (OS)
• Objective Response Rate
• The Number of Participants Who Experienced at Least One Grade 3 or Higher Adverse Event Deemed at Least Possibly Related to Treatment (Toxicity)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event measure. Each participant contributes information from randomization until documented progression or death, or until follow-up ends without either event being recorded. Kaplan-Meier methods estimate the event-free pattern over follow-up while accounting for participants whose event time is not observed during the assessment period. The median is read from that estimated curve at the point where the estimated event-free proportion reaches one half. It is not an arithmetic average of individual observed times.

What does the log-rank test compare?

The log-rank test evaluates whether event timing differs between the randomized groups over the observed follow-up. It uses information from the sequence of events and the number of participants still under observation at each event time. The registry specifies an unstratified log-rank test, meaning the listed primary comparison does not describe adjustment through stratification factors. The registry states that the p-value would be used for the superiority decision at a one-sided level of 0.10. A p-value describes how unusual the data, or more extreme data, would be under the test's null hypothesis and assumptions; it is not the probability that the null hypothesis is true.

What does the hazard ratio represent?

The registry specifies a Cox proportional hazards model for estimating the PFS hazard ratio. The reported hazard ratio compares the estimated event hazard in the atezolizumab group with that in the placebo group. A value below 1 indicates a lower estimated hazard in the first group under this model; a value above 1 indicates a higher estimated hazard. This is a relative time-to-event measure, not a ratio of median times or a direct statement about how many participants experienced progression.

The Cox model is generally interpreted under a proportional-hazards assumption: the relative hazard between groups is treated as constant over time. Whether that assumption was checked, and what diagnostic results were obtained, are not reported in the registry record. If relative hazards change over follow-up, a single hazard ratio can be an incomplete summary. The log-rank test and Cox estimate are related approaches to comparing event-time patterns, but they answer their questions through different summaries.

How should a confidence interval be read?

A confidence interval expresses statistical uncertainty around an estimate under the method used. A narrower interval indicates greater precision than a wider interval, all else equal. For the hazard ratio, an interval that includes 1 does not rule out no relative hazard difference at the confidence level used. The interval also retains values on either side of 1, so it reflects uncertainty about both the direction and size of the relative effect. A confidence interval is not a range containing a stated proportion of individual participants' outcomes.

The registry reports medians with 95% confidence intervals as well as a 95% interval for the hazard ratio. Median intervals describe uncertainty about each arm's median; they are not themselves the direct test of the between-arm contrast. The hazard-ratio interval pertains to that relative contrast under the Cox model. It is therefore important not to substitute overlap of separate median intervals for the specified log-rank comparison.

How do the secondary-outcome methods differ?

Overall survival is another time-to-event outcome, defined from randomization to death from any cause. Its reported comparison also uses a hazard ratio and log-rank method. Objective response is a binary outcome: participants are classified according to whether a response was recorded during the assessment period. The sponsor's reported objective-response comparison used Fisher's exact test. This test evaluates evidence of an association in a two-group categorical comparison, and it does not use event timing in the way a survival analysis does.

Different outcome types require different summaries. A median and hazard ratio describe event-time outcomes; a response proportion describes the share meeting a response definition. The registry lists confidence intervals for the arm-level response percentages. An unadjusted re-calculation of the response comparison is not a substitute for the sponsor's reported analysis. No discrepancy is identified in the registry record, and the reported analysis remains the relevant sponsor result.

General statistical interpretation also depends on assumptions and data handling. For survival methods, censoring should be understood as ending observation without an event being recorded, not as proof that the event will never occur. The registry does not report details about censoring rules, missing outcome data, or sensitivity analyses. For the objective-response comparison, it does not report how missing assessments were classified. Those omissions limit what can be concluded about robustness from the registry record alone.

11. Confidence Intervals and Precision

The primary PFS hazard-ratio estimate is 0.725, and its 95% confidence interval runs from 0.491 to 1.07. Because the interval includes 1, the results are compatible with no relative hazard difference as well as with effects in either direction within the interval. The estimate itself lies below 1, but its precision is limited enough that the interval extends above 1. This is why the point estimate should not be read as a complete description of uncertainty.

The median PFS estimates are 4.37 months, with a 95% confidence interval from 4.07 to 6.41, for the atezolizumab regimen, and 3.32 months, with a 95% confidence interval from 2.14 to 6.21, for the placebo regimen. These intervals convey uncertainty around each median separately. They do not directly test the randomized contrast, and their overlap should not be used as a replacement for the reported log-rank result.

For overall survival, the reported hazard ratio is 0.94 with a 95% confidence interval from 0.56 to 1.56. The interval is broad and includes 1. The arm-specific median estimates are 10.55 months and 10.61 months. The reported lower confidence limits are 8.21 and 8.8 months; the upper limits are not reported in the registry record. The absence of an upper limit in the posted results means precision cannot be fully described from both ends of those median intervals.

Objective-response intervals are also broad: 3.5 to 16.8 for the atezolizumab group and 0.53 to 14.84 for the placebo group, expressed as percentages in the registry. Such breadth indicates substantial uncertainty about the response proportions and the contrast. Across endpoints, confidence intervals help distinguish an estimated effect from the range of values still compatible with the data and method. They do not address every source of uncertainty, including missing data, model assumptions, or multiplicity.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design calculations. The original sample-size justification and design assumptions are not reported in the registry record. For time-to-event outcomes, the listed figures are total events required across the study, calculated using the Schoenfeld approach. For the other outcomes, the figures are participants per arm.

The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider effects at 100%, 75%, and 50% of the observed effect. The 80% power column describes the number of events or participants needed under those assumptions for an 80% chance of detecting the specified effect if that effect is present. The 90% power column describes the corresponding requirement for a 90% chance. Power is a property of a planned study under assumed conditions, not a probability that a particular result is true.

Smaller effects require more information to distinguish them from random variation, so the illustrations increase as the assumed effect becomes a smaller fraction of the observed effect. For binary outcomes, the figures refer to participants in each arm; for survival outcomes, they refer to total events, not participants. The event totals therefore cannot be read as target enrollment without assumptions about how many participants will experience an event during follow-up.

These are planning illustrations, not observed power. They should not be used to explain the trial's result as a consequence of being adequately or inadequately powered, because they use the observed effect and do not represent the trial's original design basis. The registry record does not report the original sample-size assumptions.

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 = 0.725, so ln(HR) = -0.3216.
2. d = 4 × (1.96 + 0.842)² / [ln(0.725)]² = 303.6, rounded up to 304 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 <- 0.725                              # 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(2873195)
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 = 304 (80% power), 407 (90% power)
 75% of observed effect: events = 540 (80% power), 723 (90% power)
 50% of observed effect: events = 1,215 (80% power), 1,626 (90% power)
Simulated power with 304 events: 0.780 (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 435 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 133 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 <- 3.32          # control-arm median, months (converted from the posted unit)
hr          <- 0.725          # 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: 234         p (1-sided)   0.0001
 Events: 137        ~HR at bound   0.5304
   Month: 13    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.72   0.0338
   IA 2: 67%                   Z   2.5114
      N: 386         p (1-sided)   0.0060
 Events: 274        ~HR at bound   0.7382
   Month: 21    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.72   0.5603
       Final                   Z   1.9930
      N: 436         p (1-sided)   0.0231
 Events: 411        ~HR at bound   0.8215
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.72   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 registry's sponsor-reported primary analysis is the log-rank comparison, with a hazard ratio of 0.725, a 95% confidence interval from 0.491 to 1.07, and p = 0.051. The primary analysis description also specifies a Cox model for the hazard ratio and Kaplan-Meier methods for medians. These are the sponsor's posted results for the randomized PFS comparison.

No discrepancy is flagged between the sponsor-reported result and the registry's presentation. Where a recalculated summary is available for an outcome, it is an unadjusted calculation from posted summary statistics and does not replace the sponsor's analysis. In particular, an independently derived comparison should not be treated as a correction to the sponsor result when the registry does not identify a discrepancy. The sponsor's own analysis takes precedence if a discrepancy is present.

The objective-response outcome includes a sponsor-reported Fisher exact p-value. That test result is distinct from a simple unadjusted comparison reconstructed from the response counts, and the registry's sponsor-reported result is the appropriate reported analysis to quote. The record does not provide further detail about the analysis dataset, model diagnostics, or missing-data procedures, so those cannot be used to reconcile or reinterpret the posted estimates.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies PFS as the primary outcome and describes a superiority comparison using an unstratified log-rank test at a one-sided significance level of 0.10. It states that the p-value would be used for decision-making. The record also lists overall survival, objective response, and toxicity as secondary outcomes. It does not report a multiplicity-control procedure, such as an adjustment across secondary tests, or a hierarchy specifying how those outcomes should be tested. Without that information, secondary p-values should not be treated as though they were protected against the increased chance of false-positive findings from multiple comparisons.

The primary analysis population is described as modified intent-to-treat. The registry does not define which randomized participants were included or excluded from that population. The reported PFS analysis counts are 82 and 46 by arm, while overall enrollment is 133. The record does not explain the differences among those counts, so no reason for them should be inferred.

Missing-data handling is not reported in the registry record. In a time-to-event analysis, follow-up that ends before progression or death can be censored, but the registry does not give the detailed censoring rules or report how missing assessments were handled. It also does not describe missing-data handling for objective response. These gaps prevent a full assessment of whether the estimates could be sensitive to missing or incomplete outcome information.

The registry specifies the log-rank test, Cox model, and Kaplan-Meier methods for PFS, but model diagnostics and checks of the proportional-hazards assumption are not reported. Details of any interim analyses, protocol changes relevant to analysis, or sensitivity analyses are also not reported in the registry record. These are uncertainties in the available reporting; they do not establish that such procedures were or were not undertaken.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death nos (8.6%), hypertension (7.4%), fever (4.9%), abdominal pain (4.3%), gastrointestinal disorders - oth spec (4.3%).

The adverse-event results report serious-event counts among 81 participants at risk in the atezolizumab group and 46 at risk in the placebo group. At least one serious adverse event was recorded for 36 participants in the atezolizumab group and 12 in the placebo group. The registry also reports other adverse-event counts of 77 and 42 among the respective groups at risk. These are counts from the posted safety record and should not be interpreted as causal comparisons without additional analysis.

The most frequently listed serious-event terms include Death NOS, hypertension, fever, abdominal pain, gastrointestinal disorders - other specified, and sepsis, with percentages reported for each term. A term such as Death NOS is an adverse-event classification and does not by itself establish that a death was caused by treatment. The registry record does not provide a treatment-related causal interpretation for each listed event term.

There were 45 deaths recorded in the atezolizumab group and 23 in the placebo group in the adverse-event information. Those counts are not equivalent to treatment-related deaths and should not be read as a direct comparison of mortality risk without accounting for follow-up and the relevant outcome analysis. The registry lists toxicity as a secondary outcome, but further details of event collection, exposure time, and comparative safety analysis are not reported in the registry record.

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

The results describe a randomized comparison of adding atezolizumab to capecitabine and bevacizumab against using placebo with the same listed background regimen. For PFS, the estimated hazard ratio is below 1, while its 95% confidence interval includes 1. The reported p-value is 0.051, and the registry's stated decision framework uses a one-sided significance level of 0.10. These features should be considered together: the point estimate favors a lower estimated event hazard in the atezolizumab group, but the confidence interval indicates uncertainty about the direction and size of the relative effect.

The median PFS estimates are arm-specific summaries, not predictions for an individual. They do not show how every participant's disease course unfolded, and they do not indicate that all participants were followed for the same length of time. The analysis is based on the modified intent-to-treat population, whose definition is not further explained in the registry record.

The secondary outcomes provide additional, but not definitive, context. Overall survival and objective response have substantial uncertainty, and the record does not report a multiplicity strategy for interpreting secondary comparisons. Safety counts describe recorded events but do not establish that a regimen caused a particular event or that the groups had equivalent exposure and follow-up.

These results do not establish a guaranteed benefit or lack of benefit for any individual, and they are not medical advice. They describe estimates from this trial population and this registry record. Generalization beyond the studied population, or conclusions about outcomes not reported, require evidence beyond these posted results. The registry does not report several details that would help assess robustness, including missing-data procedures, the definition of the modified intent-to-treat population, and model diagnostics.

19. Why This Trial Matters Statistically

This trial is statistically informative because it compares two regimens that share bevacizumab and capecitabine, with randomized assignment differing by atezolizumab versus placebo. That design makes the added-agent contrast the central estimand, while randomization supports a fair comparison on average when the analysis follows the randomized groups appropriately.

The primary outcome uses time-to-event methods rather than a single end-of-study proportion. This allows follow-up time and censoring to contribute to the analysis, and it distinguishes the estimated median from the hazard-ratio contrast. The reported PFS result also illustrates why several summaries matter: the hazard-ratio point estimate is below 1, its confidence interval crosses 1, and the registry's described decision level is one-sided. Readers need the analysis framework as well as the point estimate to understand what the result can support.

The trial also demonstrates the different evidential roles of primary and secondary outcomes. Overall survival and objective response measure distinct aspects of outcome, while toxicity records describe safety events. Secondary results can enrich interpretation, but multiple unadjusted comparisons do not carry the same confirmatory weight as a designated primary test.

Finally, the registry record makes visible limitations in what can be assessed from posted results. The modified intent-to-treat population is named but not defined; missing-data methods, proportional-hazards diagnostics, and multiplicity handling are not reported. These gaps are statistically relevant because they affect reproducibility and how confidently estimates can be interpreted, even when the main model and test are identified.

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 define the modified intent-to-treat population, so the relationship between the randomized population and the outcome analysis counts is not fully explained. Overall enrollment is 133, while the primary outcome has analysis counts of 82 and 46 by arm. The record does not explain the difference, and the counts should not be reconciled by speculation.

Important analytic details are not reported: handling of missing assessments and censoring, checks of the Cox proportional-hazards assumption, sensitivity analyses, interim analyses, and the original sample-size justification. The registry specifies a one-sided 0.10 significance level for primary decision-making but does not report a multiplicity strategy for secondary outcomes. These omissions limit independent evaluation of robustness and confirmatory status.

Several posted estimates have wide confidence intervals. The PFS hazard-ratio interval includes 1, the overall-survival interval is broad and includes 1, and the response intervals are broad. The upper confidence limits for the arm-specific overall-survival medians are not reported in the registry record. These are limitations in precision and reporting, not evidence that an unreported result has a particular value.

The safety record presents event counts and selected serious-event terms, but does not report exposure-adjusted comparisons or detailed causal assessments for the terms listed. As a result, the counts alone cannot establish comparative treatment-related risk. The registry gives the assessment timeframe for the efficacy outcomes but does not provide further details about the timing and completeness of assessments.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Capecitabine and Bevacizumab With or Without Atezolizumab in Treating Patients With Refractory Metastatic Colorectal Cancer — NCT02873195.
• Registry record last updated 2024-08-23; status last verified 2024-07.
• Results first posted 2020-02-05.
• 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

BACCI was a completed, randomized, double-blind, placebo-controlled phase II trial in refractory metastatic colorectal cancer. It compared atezolizumab, bevacizumab, and capecitabine with placebo, bevacizumab, and capecitabine. The registry lists enrollment of 133 and identifies PFS as the primary endpoint, assessed from randomization to progression or death.

The primary analysis used a log-rank comparison, with the reported hazard ratio estimated at 0.725 and a 95% confidence interval from 0.491 to 1.07. The registry describes a one-sided 0.10 decision level and reports p = 0.051. Overall survival and objective response are among the secondary outcomes. The record does not report several details needed for a fuller assessment of analysis populations, missing data, multiplicity, and model assumptions.