A Study of Avastin (Bevacizumab) and Xeloda (Capecitabine) as Maintenance Treatment in Patients With Metastatic Colorectal Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Avastin (Bevacizumab) and Xeloda (Capecitabine) as Maintenance Treatment in Patients With Metastatic Colorectal Cancer (NCT00623805), a randomized phase 3 study. The primary outcome is Progression-free Survival.

2. Clinical Question

The comparison concerns treatment strategies, not the isolated effect of a single medicine: participants assigned to the maintenance strategy received the initial combination before moving to maintenance. The results therefore describe the trial’s randomized strategies as recorded, rather than separating the effect of each drug or treatment phase. The study was randomized, open label, parallel group and phase III. The registry record identifies the condition as colorectal cancer and describes the population as people with metastatic colorectal adenocarcinoma in the official title. It does not report a more detailed clinical question about subgroups or treatment-effect variation in the posted endpoint information.

3. Trial Design

The registry record describes a randomized, multicenter phase III parallel-group study with no masking. It was marked completed. Enrollment was 123. Participants were assigned to continue bevacizumab, capecitabine and oxaliplatin until disease progression, or to receive that combination for 6 3-week cycles and then continue bevacizumab and capecitabine until disease progression. The registry summary describes the doses as bevacizumab 7.5 mg/kg intravenously on Day 1 of each cycle, oxaliplatin 130 mg/m^2 intravenously on Day 1, and capecitabine 1000 mg/m^2 orally twice a day on Days 1-14.

The trial started in 2008-03, and primary completion was recorded in 2012-05. The primary endpoint timeframe is baseline to the end of the study, described as up to 4 years, 2 months. The primary analysis population is defined in the registry as the intent-to-treat population: all randomized participants who had at least 1 post-randomization efficacy assessment. The posted arm summaries list 62 participants for continued combination treatment and 61 for the strategy followed by maintenance. The record does not explain the difference between enrollment and the endpoint population counts, or give further accounting of participants included in each analysis.

The design makes the treatment-strategy contrast clinically interpretable as a comparison between continuing the full combination and withdrawing oxaliplatin after the initial treatment period while continuing the other two medicines. Because the study was unmasked, participants and study personnel were not blinded to assigned strategy, according to the registry’s masking classification. The record does not report details of allocation concealment, stratification, the randomization procedure, center-level analysis, or protocol deviations. The trial’s original sample-size justification and its prespecified statistical analysis plan are not reported in the registry record, so the posted means and unadjusted recalculations should not be mistaken for a full account of the sponsor’s planned analysis.

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: Intent-to-treat population: All randomized participants who had at least 1 post-randomization efficacy assessment.

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: Intent-to-treat population: All randomized participants with a least 1 post-randomization efficacy assessment.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival, measured over Baseline to the end of the study (up to 4 years, 2 months).

Progression-free survival is the time from the first administration of study drug to the first documented disease progression or death, whichever occurs first. It combines two clinically important events into a time-to-event endpoint: progression documented under the trial’s lesion criteria, or death. The registry description defines progression using target and non-target lesions. For target lesions, it specifies at least a 20% increase in the sum of the longest diameter, using the smallest sum recorded since treatment started as the reference; it also allows unequivocal progression of existing non-target lesions to define progression.

The trial’s description says measurable lesions were selected at baseline for repeated measurement and that a baseline sum of their longest diameters was calculated. This makes progression assessment dependent on repeated disease evaluation as well as the timing of death. The registry reports the primary endpoint in months as a mean with a standard error, rather than presenting a median or a hazard ratio in the posted summary. A mean provides an average time in the analyzed population, but by itself does not show the shape of the time-to-event distribution or how survival probabilities changed over follow-up. The endpoint is used to compare the duration participants remained alive without documented progression under the assigned strategies. The registry record does not report further details about assessment schedules or censoring rules.

7. Results Posted in the Registry

• Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C: mean 12.60 versus 9.00 on control; difference 3.60 (95% CI 1.21 to 5.99), standardized effect d = 0.53; z-test p = 0.003.

8. Secondary Efficacy Endpoints

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

Overall Survival

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C: mean 25.40 versus 21.00 on control; difference 4.40 (95% CI 0.21 to 8.59), standardized effect d = 0.37; z-test p = 0.040.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With a Complete Response or a Partial Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C: 59.0% (36/61) versus 53.2% (33/62) on control; risk difference 5.8 percentage points (95% CI -11.7 to 23.3), risk ratio 1.11 (0.81–1.52); unadjusted two-proportion z-test p = 0.518.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C and the control. The interval gives the range of effects that remain compatible with the data.

Time Until a Complete Response or a Partial Response

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C: mean 2.90 versus 3.50 on control; difference -0.60 (95% CI -1.76 to 0.56), standardized effect d = -0.25; z-test p = 0.310.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bevacizumab(B)+Capecitabine(C)+Oxaliplatin Followed by B+C and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover overall survival and response, along with further response characteristics and surgical outcomes. The posted information includes results for overall survival, the percentage with a complete or partial response, and time until such a response. The registry lists additional secondary outcomes for duration of response and surgery-related measures, but their results are not reported in the registry record. This leaves the available secondary evidence incomplete relative to the outcomes listed.

At a broad level, the posted overall-survival and response summaries do not have the same degree of statistical certainty. The recalculated overall-survival comparison has an unadjusted p-value of 0.04 and a confidence interval for the mean difference from 0.205 to 8.595 months. For the response percentage, the unadjusted risk-difference interval includes zero and the p-value is 0.518. The time-to-response comparison also has an interval that includes zero and an unadjusted p-value of 0.31. These are distinct outcomes with distinct meanings, and they do not independently establish or refute the primary progression-free survival result.

Secondary outcomes can help describe whether the overall pattern of results is coherent, but they are usually less definitive when several outcomes are examined and no multiplicity strategy is reported. Without adjustment, a nominally small p-value among multiple comparisons may arise by chance. The registry record does not report whether these outcomes were confirmatory, how their analysis was prioritized, or whether multiplicity was controlled. Nor does it report sponsor inferential analyses for these posted secondary comparisons. The comparisons are simple unadjusted recalculations from posted summaries. They should therefore be treated as supporting context with uncertainty, not as conclusive confirmation of a treatment effect or as a replacement for the primary endpoint.

The secondary outcomes also differ in the participants contributing to each summary. Response timing is reported among participants with a complete or partial response, whereas the broader endpoint population is defined differently. This means that secondary summaries may describe selected subsets and should not be compared as though they all represented the same population. The registry record does not report additional details on missingness or participant flow for these outcomes. Their relationship to the primary result is consequently descriptive: they offer other views of survival and tumor response, but the reported information does not support a unified or multiplicity-adjusted conclusion across all outcomes.

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

• Overall Survival
• Percentage of Participants With a Complete Response or a Partial Response
• Time Until a Complete Response or a Partial Response
• Duration of Response
• Percentage of Participants With Metastatic Lesions Previously Considered Inoperable Who Became Operable and Underwent Surgery
• Percentage of Participants With a R0 Resection

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous summary measured in months. The registry gives an arm mean and standard error for each strategy. A mean describes the average observed outcome in the analyzed group. The standard error describes uncertainty in the estimated mean; it is not the spread of individual participants’ progression-free survival times. Individual outcomes can vary substantially even when a mean is estimated with some precision. The standard error therefore answers a different question from a standard deviation, which describes participant-level variability.

What does the mean difference represent?

The posted comparison subtracts the mean for continued combination treatment from the mean for the maintenance strategy. The reported unadjusted mean difference is 3.6 months. A positive value indicates a higher mean for the maintenance strategy in this contrast. The recalculation uses the posted arm summaries, rather than an individual-participant model or an adjustment for baseline characteristics. The registry record does not report an inferential analysis from the sponsor for this endpoint, so the calculated contrast should be read as a simple unadjusted comparison, not as a substitute for an unreported prespecified model.

Randomization is intended to make assigned groups comparable, on average, with respect to factors measured and unmeasured at baseline. It does not guarantee that every characteristic is balanced in a particular trial, especially when group sizes are limited. An unadjusted comparison is transparent and closely tied to the reported arm summaries, but its precision and interpretation depend on those summaries and the analysis population. The registry record does not report covariate adjustment, stratification factors, or other modeling details for the primary outcome.

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

A confidence interval gives a range of values that are reasonably compatible with the observed data under the calculation’s assumptions. It helps convey both the direction and uncertainty of an estimated difference. The primary mean-difference interval is 1.208 to 5.992 months. Because the interval does not cross zero, it is consistent with a positive mean difference under this unadjusted calculation. The p-value, p = 0.003, describes how unusual data at least as inconsistent with a no-difference assumption would be under the calculation’s model. It is not the probability that the null hypothesis is true, and it does not measure clinical importance.

The primary comparison is labeled as a mean difference and includes a confidence interval and an unadjusted p-value. Those quantities are recalculated from posted summary statistics. The record does not report a sponsor analysis to compare with this calculation. More generally, a statistical test depends on assumptions about the data and the sampling process. For time-to-event endpoints, methods often account for censoring and use the timing of events rather than reducing the data to a mean. The registry record does not report such an analysis for the primary endpoint, nor does it report the event count or censoring details. The posted summary should therefore be interpreted as a mean-based comparison and not as evidence that a particular time-to-event model was used.

Why can distribution and follow-up matter?

Time to progression or death is usually not distributed symmetrically: some participants may have an event relatively early, while others remain event-free longer or have follow-up ending before an event is recorded. In general, this can make a mean sensitive to long observed times and to how follow-up and censoring are handled. A median, a survival curve, or a hazard ratio can answer related but distinct questions. None of those summaries is reported for the primary outcome in the registry information used for this interpretation. This is not a claim that the trial’s original analysis omitted them; their reporting is not reported in the registry record.

Over-dispersion is a general concern when outcome variation is greater than a model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow; if it allows for the actual variability, uncertainty can be larger. The registry’s primary summary reports standard errors, but it does not report a distributional diagnostic or a model addressing over-dispersion. No conclusion about whether over-dispersion occurred can be made from the posted means and standard errors alone.

What is the role of the analysis population?

The primary population is described as all randomized participants who had at least 1 post-randomization efficacy assessment. This is a registry definition of the group included in the endpoint, and it is not identical in wording to an analysis that includes every randomized participant regardless of assessment availability. The record does not report how many randomized participants lacked an efficacy assessment, why any assessments were missing, or how missing outcomes were handled. Missing data can affect an estimate if the participants with observed outcomes differ systematically from those without outcomes. The direction and size of any such effect cannot be inferred without additional information.

The posted secondary calculations also use unadjusted comparisons, and the record does not report formal multiplicity control. When many outcomes are examined, the chance of at least one apparently notable result can increase. This general issue is why secondary comparisons are often interpreted more cautiously unless they were prespecified, analyzed with an appropriate multiplicity strategy, and supported by a complete analysis plan. The registry record does not report those details. Accordingly, the primary and secondary statistics should be read according to their stated endpoint definitions and the limited analysis information available, without inferring unreported methods.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 3.6 months, and its 95% confidence interval extends from 1.208 to 5.992 months. The interval is entirely above zero, which indicates that the recalculated contrast is directionally positive across the interval. It nevertheless spans a range of possible magnitudes, so the point estimate should not be treated as the exact effect. Confidence intervals are a way to express sampling uncertainty under the calculation’s assumptions; they do not include every source of uncertainty, such as bias from missing outcome data, limitations in outcome measurement, or differences between the posted calculation and the original analysis plan.

The standard errors for the arm means are 0.7 months for continued combination treatment and 1.0 months for the strategy followed by maintenance. These quantify uncertainty in the estimated group means, rather than the range of individual participants’ outcomes. The registry does not report a confidence interval for each arm mean, but it reports the interval for their unadjusted mean difference. That interval is the more direct measure of precision for the contrast.

The record does not provide a confidence interval from a sponsor-reported primary analysis, and the recalculated interval is based on summary statistics rather than individual participant data. It also does not report the censoring pattern, event count, survival probabilities over time, or a hazard-ratio estimate. These omissions limit assessment of how the mean difference relates to the full time-to-event experience. The result is therefore statistically distinguishable from zero in the posted unadjusted calculation, but its exact magnitude and robustness to other reasonable methods are not established by the registry summary alone. Statistical precision is not the same as clinical importance; the registry record does not report a threshold for a clinically meaningful difference.

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 describe illustrative sample sizes for detecting selected fractions of the observed effect. They are planning calculations based on the observed result, not a record of the trial’s original sample-size design. For these continuous mean comparisons, the figures are participants per arm, not total events. The distinction matters because some planning displays for time-to-event outcomes report total events, whereas these figures are explicitly expressed as participants per arm.

The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The rows for planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the assumed size of the difference changes the participant requirement. The columns for 80% and 90% power describe the probability, under the planning assumptions and a specified true effect, of detecting a difference using the chosen significance threshold. The 90% power target is more demanding than the 80% target and generally requires more participants for the same effect.

The displayed planning values show that smaller effects require more participants per arm than larger effects. This is a general property of statistical power: a smaller signal is harder to distinguish from random variation, so more information is needed. The values are planning illustrations derived from the observed effect, not observed power. Observed power is not a useful substitute for interpreting the confidence interval and data after a trial; these calculations instead illustrate hypothetical future planning under stated assumptions. The trial’s original design assumptions, including its own sample-size justification, are not reported in the registry record.

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

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 3.600; pooled standard deviation σ = 6.750.
2. n = 2 × (1.96 + 0.842)² × 6.750² / 3.600² = 55.2, rounded up to 56 participants per arm 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
delta <- 3.6                      # observed difference in means
sigma <- 6.7500719310523                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(623805)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 56 (80% power), 74 (90% power)
 75% of observed effect: n per arm = 99 (80% power), 132 (90% power)
 50% of observed effect: n per arm = 221 (80% power), 296 (90% power)
power.t.test: 56.2 
Simulated power at n = 56 per arm: 0.795 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses several outcomes, comparisons, subgroups, or analysis choices. If each is tested separately without adjustment, the overall chance of at least one false-positive finding can be greater than the error rate for an individual test. This does not mean that any particular result is false; it means that isolated p-values need context when many hypotheses are considered. The registry lists several secondary outcomes in addition to progression-free survival, including overall survival, response outcomes, and surgical outcomes.

The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or which secondary analyses were intended to be confirmatory. It reports no sponsor analyses for the posted secondary outcomes. The p-values and intervals described for these outcomes are unadjusted recalculations from posted summaries. Their interpretation should account for the possibility of multiple testing and should not treat a nominal p-value as definitive evidence without a prespecified analysis framework.

Missing-data handling is another important uncertainty. The primary endpoint population is described as all randomized participants who had at least 1 post-randomization efficacy assessment. The record does not report how many randomized participants lacked such an assessment, the reasons for missing assessments, or how missing efficacy data were treated. It also does not report detailed participant flow or missing-data methods for the secondary endpoints. In general, missing data can bias a comparison when availability of an outcome is related to prognosis or treatment experience. The available record does not establish whether that occurred or how it might have affected the findings.

The phrase intent-to-treat is used in the registry’s definition of the primary population, but the stated eligibility for that population requires a post-randomization efficacy assessment. The record does not explain whether any randomized participants were excluded from the endpoint analysis or how such exclusions were addressed. It also does not give details of censoring for progression-free or overall survival. These details matter because time-to-event analyses depend on both observed events and the handling of participants whose event status is not observed by the end of follow-up. The trial’s original statistical plan, interim analyses, and sample-size justification are not reported in the registry record. No assumptions about these methods should be inferred from the posted summaries.

15. 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: clinical worsening (3.3%), diarrhea (3.3%), urinary tract infection (3.3%), abdominal pain (1.6%), angina pectoris (1.6%).

The registry reports serious adverse events for each treatment strategy using an affected-participant count and an at-risk count. Serious adverse events were reported for 12 of 62 participants in the continued-combination group and 21 of 61 participants in the group that moved to bevacizumab and capecitabine maintenance. These are descriptive counts, not a randomized comparison adjusted for follow-up or other factors. The record does not report a statistical test or confidence interval for this safety contrast.

The listed serious adverse-event terms include clinical worsening, diarrhea and urinary tract infection, each reported as 3.3%. Abdominal pain, angina pectoris and anorexia are each listed as 1.6%. These percentages describe the reported terms, not a complete account of every possible safety outcome. The record also gives counts for other adverse events affecting participants, but these aggregate counts do not communicate severity, duration, recurrence or treatment attribution.

Deaths are not reported in the registry record’s safety summary. The registry information does not provide enough detail to determine whether an event was caused by treatment or to compare safety risks while accounting for exposure time. The figures should be read as the adverse-event reporting available in the record, rather than as a comprehensive safety assessment.

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

The registry’s primary summary reports a higher mean progression-free survival in the group that received bevacizumab and capecitabine maintenance after initial combination treatment than in the group that continued the three-drug combination. The unadjusted recalculated difference is 3.6 months, with a 95% confidence interval from 1.208 to 5.992 months and p = 0.003. Those statistics describe the posted endpoint summary and its uncertainty under the calculation; they do not establish what any individual participant experienced.

The result applies to the treatment strategies as compared in this trial. It does not isolate the contribution of bevacizumab, capecitabine, or oxaliplatin, because the groups differed in their planned treatment after the initial combination period. It also does not show that every participant would have a longer progression-free time with one strategy. Group averages can differ while individual outcomes vary, and the registry summary does not give the distribution of individual times or time-specific probabilities.

A statistical difference does not by itself establish clinical importance. The registry record does not report a threshold for a clinically meaningful difference, patient-reported outcomes, or a detailed account of treatment burden. Nor does the posted mean comparison provide the hazard ratio, median progression-free survival, or survival probabilities that would describe other aspects of time-to-event outcomes. The confidence interval describes statistical uncertainty under the unadjusted calculation, not uncertainty from every possible source of bias or measurement limitations.

The secondary results offer additional but incomplete context. The overall-survival and response summaries have their own estimates and uncertainty, and the record does not report multiplicity adjustment or sponsor analyses for these outcomes. Results for some listed secondary outcomes are not reported in the registry record. Safety information is similarly limited to the posted adverse-event counts and terms; deaths are not reported in the registry record. These limitations prevent a comprehensive assessment of benefit and harm from these summaries alone.

The fairest interpretation is therefore narrow: the posted summary statistics support a positive unadjusted difference in mean progression-free survival for the maintenance strategy in this trial’s defined endpoint population. They do not, by themselves, establish the robustness of that estimate under the trial’s original analysis plan, the clinical importance of its magnitude, or the full balance of benefits and harms. The sponsor’s own analysis would take precedence if reported; no such analysis is reported in the registry record for this endpoint.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares treatment strategies that share an initial combination phase but differ in whether oxaliplatin continues afterward. That structure makes the estimand a strategy-level contrast. The result cannot be attributed to a single component medicine without additional assumptions or a design that separately varies those components. Recognizing what was randomized is essential to interpreting the reported mean difference correctly.

The primary endpoint is defined as time from study drug initiation to progression or death, yet the registry posts mean months and standard errors rather than a full time-to-event analysis. This illustrates why endpoint definition and statistical summary are not interchangeable. A mean can summarize an average, but time-to-event interpretation also depends on the pattern of events, follow-up and censoring. The registry record does not report the detailed analysis needed to evaluate those features. Readers can therefore distinguish the posted numerical contrast from the broader clinical picture that other survival summaries might convey.

The record also illustrates the difference between an outcome result and its provenance. The primary mean difference, confidence interval and p-value are unadjusted recalculations from the posted arm summaries; the registry does not report the sponsor’s inferential analysis. The distinction matters because the planned statistical model, missing-data rules and multiplicity strategy can affect interpretation. These details are not reported in the registry record and should not be reconstructed from the observed values.

Finally, the endpoints do not all carry equal evidential weight. A primary result has a defined role in the trial, while several secondary outcomes create multiplicity concerns and may describe different participant subsets. Where secondary findings are unadjusted and other listed results are absent, they provide context rather than a single confirmatory narrative. Separating effect size, precision, analysis provenance and clinical importance is central to sound statistical reading of this trial.

18. 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 trial-specific limitations follow from the way the registry reports the results. The primary outcome is a time-to-event measure, but the available summary presents mean progression-free survival and standard errors. It does not report a hazard ratio, median, survival probabilities, event counts, censoring details, or the analysis method used by the sponsor. This makes it difficult to assess whether the mean captures the time-to-event pattern adequately or how the result depends on follow-up.

The primary population is described as randomized participants with at least 1 post-randomization efficacy assessment. The registry does not explain how participants without an assessment were handled or whether any were excluded from the endpoint analysis. It also does not report missing-data methods, protocol deviations, or detailed participant flow. These omissions matter for evaluating the effect of unavailable outcome assessments and the distinction between the stated population and all randomized participants.

The reported inferential comparisons are unadjusted recalculations from summary statistics. The registry does not report the sponsor’s primary analysis, its covariate structure, or the prespecified analysis plan. The discrepancy flag is false, but that does not supply missing details about the sponsor’s methods. The record also does not report multiplicity control or confirmatory status for the secondary outcomes. As a result, the secondary p-values should be interpreted cautiously.

The safety summary provides serious adverse-event counts and selected terms, but not a full account of event timing, exposure-adjusted rates, attribution, severity patterns, or deaths. Some listed secondary outcomes have no posted results in the registry record. Finally, the original sample-size justification and design assumptions are not reported; the planning figures based on the observed effect are illustrations and cannot reconstruct the original design. These limitations concern reporting available in the registry and do not establish that the trial itself omitted these analyses or procedures.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Avastin (Bevacizumab) and Xeloda (Capecitabine) as Maintenance Treatment in Patients With Metastatic Colorectal Cancer — NCT00623805.
• Registry record last updated 2014-08-08; status last verified 2014-07.
• Results first posted 2014-08-08.
• 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.

22. Record Summary

NCT00623805 is a completed randomized, multicenter phase III parallel-group study with no masking. It compared continued bevacizumab, capecitabine and oxaliplatin with an initial course of the combination followed by bevacizumab and capecitabine maintenance. The primary endpoint was progression-free survival, reported as mean months and standard errors for the intent-to-treat population defined as randomized participants with at least 1 post-randomization efficacy assessment.

The posted primary means were 9.0 months and 12.6 months. An unadjusted recalculation gives a mean difference of 3.6 months, with a 95% confidence interval from 1.208 to 5.992 months and p = 0.003. The registry record does not report the sponsor’s inferential analysis or the original statistical plan. Secondary and safety summaries are available in part; multiplicity methods, missing-data handling and several further outcome results are not reported in the registry record.