A Study of Bevacizumab (Avastin®) in Combination With Temozolomide and Radiotherapy in Participants With Newly Diagnosed Glioblastoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Bevacizumab (Avastin®) in Combination With Temozolomide and Radiotherapy in Participants With Newly Diagnosed Glioblastoma (NCT00943826), a randomized phase 3 study. The primary outcome is Co-Primary: Progression-free Survival (PFS) as Assessed by Investigator.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, multicenter phase III trial with a parallel-group design. The registry identifies quadruple masking, but does not specify in the record which roles were masked. Random assignment placed participants in one of two groups: bevacizumab with radiotherapy and temozolomide, or placebo with radiotherapy and temozolomide. The study is listed as completed, with enrollment of 921.

The common treatment backbone began with concurrent radiotherapy and temozolomide. The brief description specifies radiotherapy at a total dose of 60 Gy, administered in 2 Gy fractions, 5 days per week, and temozolomide at 75 mg/m^2 daily for 6 weeks. After a 4 week treatment break, maintenance treatment paired temozolomide with bevacizumab or placebo for 6 cycles, or until disease progression or unacceptable toxicity. After maintenance, bevacizumab or placebo monotherapy continued until disease progression. The record also describes bevacizumab dosing during these phases.

The primary endpoint was progression-free survival assessed by investigators, with follow-up from randomization until a progression-free survival event. The stated data cutoff was 31 March 2012, with follow-up reported as up to 31.4 months. Participants without a progression-free survival event were censored at their last disease assessment. The primary population was intent to treat. The registry lists secondary outcomes that include independent-review progression-free survival, overall survival estimates, quality-of-life-related progression-free survival, and adverse events.

The registry record does not report the original sample-size justification, the trial's full statistical analysis plan, interim-analysis procedures, or the details of how masking was implemented. These omissions limit what can be said about the design rationale and analysis decisions beyond the information explicitly recorded.

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: The primary completion date for co-primary outcome of Progression-Free Survival (PFS) was 31 Mar 2012, whereas, the primary completion date for co-primary outcome of Overall Survival (OS) was 28 Feb 2013. Data for PFS and OS are reported according to these cut-off dates.

Concurrent Phase

Reasons for not completing this period:

Maintenance Phase

Reasons for not completing this period:

Monotherapy Phase

Reasons for not completing this period:

After Primary Overall Survival Analysis

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat 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.

Population: Intent to treat population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Co-Primary: Progression-free Survival (PFS) as Assessed by Investigator, measured over Randomization until PFS Event [Until data cutoff= 31 March 2012 (up to 31.4 months).

Progression-free survival measures the time from randomization until disease progression or death. It combines these events into a time-to-event outcome, so the analysis reflects both how often events occur and when they occur. A median is the time by which half of the analyzed population has experienced an event, subject to the survival-analysis methods and censoring used in the analysis. It is not an average survival time and does not imply that every participant experienced an event at that time.

In this trial, investigators assessed progression using adapted Macdonald response criteria, based on radiological tumor assessments using MRI, neurological assessment, and changes in corticosteroid use. The record defines progression using findings such as an increase in the sum of products of lesion diameters compared with the nadir, unequivocal progression of existing non-index lesions, appearance of new lesions, or neurological worsening under the specified corticosteroid condition. Neurological worsening did not require a confirmatory scan. Participants without a progression-free survival event were censored at their last disease assessment.

Progression-free survival is used in trials because it captures the period without recorded progression or death, rather than waiting only for death to occur. Its interpretation depends on the event definition, timing and quality of assessments, and censoring. The registry record describes the primary endpoint as investigator-assessed and separately reports an independent review facility assessment. The record does not report details of any additional validation of the endpoint assessments.

7. Results Posted in the Registry

• Bevacizumab + RT + Temozolomide vs Placebo + RT + Temozolomide: hazard ratio 0.64 (95% CI 0.55–0.74), reported p < 0.001 (as reported in the registry).

8. Secondary Efficacy Endpoints

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

PFS as Assessed by an Independent Review Facility

• 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:
  • Bevacizumab + RT +Temozolomide vs Placebo + RT + Temozolomide: hazard ratio 0.61 (95% CI 0.53–0.71), reported p < 0.001 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Bevacizumab + RT +Temozolomide vs Placebo + RT + Temozolomide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span different questions: independent-review progression-free survival, one-year and two-year overall survival estimates, progression-free survival among participants with stable or improved health-related quality of life, and adverse events. Of these, the registry reports a quantified comparison for independent-review progression-free survival. Its direction is consistent with the primary investigator-assessed progression-free survival result. That agreement provides a related assessment of the progression endpoint, but it is not an independent confirmation of every outcome or a substitute for results on survival, quality of life, or harms.

Results for the listed one-year and two-year overall survival estimates and the quality-of-life-related progression-free survival outcome are not reported in the registry record. Consequently, an overall pattern across all secondary efficacy outcomes cannot be established from the record. The safety information is described separately and should not be treated as an efficacy endpoint.

Secondary endpoints are often interpreted with greater caution because a trial can examine several outcomes, time points, or subgroups. If many hypotheses are tested without adjustment, the chance of finding at least one nominally unusual result can increase. Whether the trial adjusted for multiplicity, or specified a hierarchy for secondary hypotheses, is not reported in the registry record. This means that any available secondary p-values should not automatically be read with the same confirmatory weight as the designated primary result. The reported secondary findings can add context, especially when they address related questions, but the unreported outcomes and unknown multiplicity approach limit the overall conclusions.

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

• PFS as Assessed by an Independent Review Facility
• Kaplan-Meier (KM) Estimate of One Year Overall Survival
• Kaplan-Meier (KM) Estimate of Two Year Overall Survival
• PFS in Participants With Stable/Improved Health Related Quality of Life (HRQoL) Based on European Organization for Research & Treatment of Cancer (EORTC) Quality of Life Questionnaire (QLQ) Core 30 (C30)(EORTC QLQ-C30) & EORTC QLQ Brain Neoplasm 20 (BN20)
• Number of Participants With Non-Serious Adverse Events, Serious Adverse Events and Death

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome. Rather than recording only whether progression or death occurred, the analysis uses the time from randomization until the first qualifying event. Participants who have not had a recorded event by their last disease assessment contribute information up to that point and are censored. Censoring means that the event time is not observed during the available follow-up; it does not mean the participant was known to remain event-free indefinitely. The registry states that participants without an event were censored at the last disease assessment.

A median time-to-event estimate describes the point at which the estimated event-free proportion reaches its midpoint. The reported medians are therefore useful for communicating a typical point on each group’s estimated progression-free survival distribution. They do not reveal the complete shape of those distributions. Two groups can have the same median but differ at other points in follow-up, so the median is best interpreted alongside the survival comparison and its uncertainty rather than as a complete summary by itself.

The primary comparison is reported as a hazard ratio and analyzed using the log-rank method. In general, a hazard is the rate at which an event occurs among participants who have not yet had the event, at a particular point in follow-up. A hazard ratio compares those rates between groups over time. It is not a risk ratio, an odds ratio, a difference in median times, or a statement about the chance that a specific participant will experience an event. The usual interpretation of one hazard ratio as a single summary of the group contrast is most straightforward when the relative hazards are reasonably stable over time. The registry record does not report whether proportional-hazards diagnostics or alternative time-varying analyses were used.

The log-rank test compares the event-time experience of the groups across follow-up, taking account of the timing of events and censoring. The reported p-value is a measure of how incompatible the observed comparison is with the null hypothesis under the test and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of the effect. The registry record reports p < 0.001 for the primary comparison and for the independent-review comparison.

The 95% confidence interval around a hazard ratio describes statistical uncertainty in the estimated relative comparison under the analysis. A narrower interval indicates greater precision than a wider interval, but the interval still reflects uncertainty and is not a range guaranteed to contain the true value. The interval for the primary hazard ratio is 0.55 to 0.74. The interval for the independent-review hazard ratio is 0.53 to 0.71. These intervals are not confidence intervals for the medians; the registry reports separate 95% confidence intervals for each median.

General methodological context: time-to-event analyses can use information from participants with different lengths of follow-up, because participants contribute until an event or censoring. Their validity depends on appropriate event ascertainment and censoring assumptions. If censoring is related to the likelihood of an event in ways not adequately accounted for by the analysis, estimates may be biased. The registry describes the censoring rule but does not report enough detail to evaluate the censoring mechanism or the completeness of follow-up.

The reported primary analysis population is intent to treat. In general, an intent-to-treat analysis retains participants in their randomized groups for the primary comparison, regardless of treatment received after randomization, helping preserve the comparison created by random assignment. The registry does not provide the full analysis population flow, the extent of treatment non-adherence, or detailed handling of every post-randomization circumstance. The group counts reported for the endpoint and the safety outcomes are not identical, and the registry does not explain all reasons for these differences.

The independent review facility assessed progression-free survival as a separate secondary outcome. Independent assessment can offer a check against possible differences in investigator assessment, but it does not remove all sources of uncertainty and does not make the two endpoint assessments identical. Their definitions, available assessments, or review procedures can affect estimates. The registry record names the independent review facility outcome but does not report the review procedures in detail.

General statistical context: estimates, tests, and confidence intervals answer related but distinct questions. A point estimate conveys the observed scale and direction of the comparison; a confidence interval conveys uncertainty around an estimate; a p-value assesses compatibility with a specified null model. None alone establishes clinical importance, generalizability, or the balance of benefits and harms. Interpretation should also consider the endpoint definition, analysis population, follow-up, censoring, and whether secondary analyses were adjusted for multiple testing.

11. Confidence Intervals and Precision

The primary median estimates have 95% confidence intervals of 10.0 to 11.4 months for the bevacizumab group and 6.0 to 7.5 months for the placebo group. These intervals show the uncertainty around each median estimate under the registry analysis. They are not intervals containing the progression-free survival times of individual participants, and overlap or separation of median intervals is not a substitute for the reported comparison test.

The primary hazard ratio is 0.64, with a 95% confidence interval of 0.55 to 0.74. This interval indicates that the estimated relative hazard is below 1 across the interval, while also showing that the effect is not known to a single exact value. The reported p-value, p < 0.001, addresses the test of the null comparison; it does not measure precision or the practical importance of the result.

For independent-review progression-free survival, the median confidence intervals are 7.9 to 9.7 months and 4.1 to 5.1 months. Its hazard ratio is 0.61, with a 95% confidence interval of 0.53 to 0.71. The estimates are directionally similar to the investigator-assessed result, but precision and measurement are specific to each analysis.

Confidence intervals are estimates of sampling uncertainty under the statistical method. They do not account automatically for every possible source of bias, such as assessment differences, missing information, or departures from model assumptions. The registry record does not report enough detail to quantify those additional uncertainties. Interpretation should therefore distinguish the relatively precise reported comparisons from broader uncertainty about measurement, analysis choices, and applicability beyond 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 planning figures for the time-to-event comparisons are total event counts, not participants per arm. They are planning illustrations based on the observed effect, not the trial's original design calculation. The original trial sample-size assumptions and justification are not reported in the registry record.

The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects set at 100%, 75%, or 50% of the observed effect. For the primary progression-free survival comparison, the total-events entries are 158 and 212 for planning at 100% of the observed effect, 281 and 376 at 75%, and 631 and 845 at 50%, corresponding respectively to the 80% and 90% power columns.

Power describes the probability that a planned study would meet its statistical significance criterion under a specified true effect and the stated planning assumptions. The 80% column represents a planning target with 80% power; the 90% column represents a higher target. These columns do not describe the probability that the observed result is true. For a time-to-event study, the figures refer to total events because the information for the comparison depends substantially on observed events, not only the number enrolled. Smaller effects require more events to detect under the same planning framework.

These figures are planning illustrations, not observed power. They should not be read as the trial's enrollment target or as a retrospective measure of how likely the observed finding was to occur. The registry record does not report the original design assumptions, so the illustration cannot establish whether the planned trial was designed around the observed 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 = 0.640, so ln(HR) = -0.4463.
2. d = 4 × (1.96 + 0.842)² / [ln(0.640)]² = 157.6, rounded up to 158 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 <- 0.64                              # 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(943826)
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 = 158 (80% power), 212 (90% power)
 75% of observed effect: events = 281 (80% power), 376 (90% power)
 50% of observed effect: events = 631 (80% power), 845 (90% power)
Simulated power with 158 events: 0.785 (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 240 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 921 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 <- 6.2          # control-arm median, months (converted from the posted unit)
hr          <- 0.64          # 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: 160         p (1-sided)   0.0001
  Events: 71        ~HR at bound   0.4141
   Month: 16    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.64   0.0338
   IA 2: 67%                   Z   2.5114
      N: 240         p (1-sided)   0.0060
 Events: 142        ~HR at bound   0.6558
   Month: 25    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.64   0.5603
       Final                   Z   1.9930
      N: 240         p (1-sided)   0.0231
 Events: 213        ~HR at bound   0.7608
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.64   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The primary comparison reported by the sponsor is a log-rank hazard ratio of 0.64, with a 95% confidence interval of 0.55 to 0.74 and p < 0.001. The posted median estimates are 10.6 months for the bevacizumab-containing group and 6.2 months for the placebo-containing group. The sponsor's hazard-ratio analysis and the median summaries describe the same primary endpoint from different statistical perspectives: the medians identify points on the time-to-event distributions, while the hazard ratio summarizes a relative event-rate comparison.

The registry record also reports the same hazard-ratio estimate and interval in its analysis details. No discrepancy is flagged between the reported comparison and the analysis record. Any simple unadjusted re-calculation from summary statistics is not a replacement for the sponsor's analysis, which uses the reported log-rank comparison. Such a re-calculation cannot reproduce all participant-level information or the full analysis procedure.

The independent-review comparison is separately reported, with a hazard ratio of 0.61, a 95% confidence interval of 0.53 to 0.71, and p < 0.001. It should not be conflated with the investigator-assessed primary analysis. The registry record does not provide further details that would support a reconstruction of the sponsor's analyses beyond the reported methods and estimates.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies investigator-assessed progression-free survival as the co-primary endpoint and lists several secondary outcomes. The record does not report a multiplicity-control procedure, a testing hierarchy, or how the co-primary designation affected the interpretation of statistical tests. Without that information, it is not possible to determine whether or how the overall chance of false-positive findings across multiple outcomes was controlled. This matters especially when interpreting secondary comparisons, since multiple tests can make nominal significance less persuasive unless the analysis plan accounts for them.

The registry record does not report interim-analysis procedures, stopping boundaries, or whether any interim results were examined. It also does not report a full statistical analysis plan, so the prespecification of analysis details cannot be independently established from this record. The absence of these details should not be taken as evidence that no such procedures existed; they are simply not reported in the registry record.

The primary endpoint population is described as intent to treat. For participants without a progression-free survival event, the record says they were censored at their last disease assessment. It does not provide a detailed account of missing assessments, reasons for loss to follow-up, or sensitivity analyses addressing missing outcome information. It also does not describe the extent of protocol deviations or how such cases were handled.

Statistical interpretation depends on both the stated estimand and the completeness of outcome information. Censoring allows participants with incomplete event follow-up to contribute observed information, but it does not eliminate uncertainty about events after the last assessment. The registry record does not provide enough detail to assess the plausibility of censoring assumptions. For the listed overall survival, quality-of-life, and other secondary outcomes, results and detailed missing-data handling are not reported in the registry record.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: thrombocytopenia (3.7%), pulmonary embolism (2.8%), deep vein thrombosis (2.4%), pneumonia (2.2%), cerebrovascular accident (1.7%).

The registry reports serious adverse events among 179 of 461 participants at risk in the bevacizumab, radiotherapy, and temozolomide group, and among 115 of 450 participants at risk in the placebo, radiotherapy, and temozolomide group. These are counts and denominators for the registry's serious adverse event reporting. They should be read using those denominators rather than the progression-free survival analysis group counts. The record does not explain the difference between these safety denominators and the endpoint group counts.

The most frequently listed serious-event terms for the bevacizumab-containing group include thrombocytopenia (3.7%), pulmonary embolism (2.8%), deep vein thrombosis (2.4%), pneumonia (2.2%), cerebrovascular accident (1.7%), and pyrexia (1.7%). The listed terms are event categories, not a complete description of all possible harms or their severity and duration.

These figures describe safety reporting in the registry and should not be interpreted as a complete comparative assessment of causation. The record does not report death counts by group in the adverse-event summary. It also does not provide enough detail to assess timing, exposure-adjusted rates, or the full clinical context of each event.

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

The primary result describes a difference in the observed progression-free survival distributions between the randomized groups under the trial's assessment rules. The bevacizumab-containing group had a reported median of 10.6 months, compared with 6.2 months in the placebo-containing group. The sponsor-reported hazard ratio was 0.64, with a 95% confidence interval of 0.55 to 0.74. The log-rank p-value was p < 0.001. These estimates provide evidence of a group-level difference in the primary time-to-event outcome in this trial.

That result does not mean that every participant in the bevacizumab group remained progression-free longer than every participant in the placebo group. Median times and hazard ratios summarize group distributions; they do not predict an individual's outcome. Nor does the primary endpoint establish an effect on overall survival, quality of life, or every other outcome considered by the trial. Results for several listed secondary outcomes are not reported in the registry record.

The hazard ratio is not a direct measure of absolute benefit and cannot be converted into an individual probability from the information. The median estimates also do not describe the entire follow-up trajectory. Interpretation depends on progression assessment, censoring, and the analysis assumptions. The record defines investigator assessment and last-assessment censoring, but does not report sufficient detail to resolve every methodological uncertainty.

Safety must be considered separately from efficacy. The registry reports serious adverse event counts and selected serious-event terms, but these do not alone establish the full balance of outcomes or causation. The results apply most directly to the trial population and treatment conditions described in the record. They do not, by themselves, settle how the regimen compares with other approaches, how effects vary among different populations, or what an individual should choose. Those questions require evidence and context beyond this registry record.

19. Why This Trial Matters Statistically

This trial illustrates how randomized comparisons can isolate the statistical contrast of adding a study drug to a shared treatment backbone. Both groups received radiotherapy and temozolomide, while bevacizumab was compared with placebo. Randomization and masking are important design features for reducing some sources of systematic difference between groups, although they do not remove all uncertainty in outcome measurement or analysis.

The primary outcome is a time-to-event measure, so its analysis uses both event occurrence and timing. The registry reports medians, a hazard ratio, confidence intervals, and a log-rank p-value. These statistics answer complementary questions: the medians give interpretable points on the event-time distributions, the hazard ratio summarizes a relative comparison, and the interval communicates uncertainty. Reading them together is more informative than relying on a p-value alone.

The independent-review progression-free survival analysis offers a second assessment of a related endpoint, with results directionally consistent with the primary assessment. At the same time, the record highlights why endpoint-specific reporting matters: overall survival and quality-of-life-related outcomes are listed but their results are not reported. A strong primary comparison cannot stand in for unreported outcomes.

The trial also demonstrates the importance of separating the design of the original study from retrospective planning illustrations. Event-based planning figures can show how required information changes when the target effect becomes smaller, but they do not reveal the assumptions that originally determined enrollment. Finally, safety counts need their own denominators and context; they should not be collapsed into efficacy conclusions. These distinctions are central to reading clinical-trial statistics carefully.

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 leaves important design and analysis details unreported. It does not give the original sample-size justification, a full statistical analysis plan, interim-analysis procedures, or multiplicity control. The planning figures are illustrations based on the observed effect and cannot establish the assumptions used to design the trial. The record also does not specify which roles were included in quadruple masking or describe how masking was maintained.

Progression-free survival depends on the criteria and timing used to identify progression. The record describes adapted Macdonald criteria and several components of assessment, but does not provide detail on assessment schedules, adjudication processes, or the handling of every ambiguous assessment. It states that participants without an event were censored at their last disease assessment, but does not report loss-to-follow-up details or sensitivity analyses for censoring and missing assessments.

The primary result concerns investigator-assessed progression-free survival. Independent review provides a related assessment, but the record does not describe the review process in enough detail to judge how closely the two assessments were aligned. The record also does not report results for several listed secondary outcomes, including the overall survival estimates and quality-of-life-related outcome. This restricts interpretation of the broader benefit and harm profile.

Safety reporting includes serious adverse event counts, selected serious-event terms, and denominators that differ from those reported for the primary endpoint. The registry does not explain the denominator differences, provide death counts in the safety summary, or present enough context to evaluate event timing or attribution. These limitations do not negate the reported primary analysis, but they constrain the conclusions that can be drawn from the registry record alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Bevacizumab (Avastin®) in Combination With Temozolomide and Radiotherapy in Participants With Newly Diagnosed Glioblastoma — NCT00943826.
• Registry record last updated 2017-09-25; status last verified 2017-08.
• Results first posted 2013-05-20.
• 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

This completed randomized, double-blind, placebo-controlled, multicenter phase III trial enrolled 921 participants with newly diagnosed glioblastoma. It compared bevacizumab plus radiotherapy and temozolomide with placebo plus radiotherapy and temozolomide. The primary endpoint was investigator-assessed progression-free survival in the intent-to-treat population.

The reported median progression-free survival was 10.6 months in the bevacizumab group and 6.2 months in the placebo group. The sponsor-reported hazard ratio was 0.64, with a 95% confidence interval of 0.55 to 0.74 and p < 0.001. An independent-review progression-free survival analysis showed a directionally consistent comparison. Several other secondary results and important design details are not reported in the registry record, limiting conclusions beyond the posted progression-free survival findings and safety summary.