Bevacizumab With or Without Radiation Therapy in Treating Patients With Recurrent Glioblastoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bevacizumab With or Without Radiation Therapy in Treating Patients With Recurrent Glioblastoma (NCT01730950), a randomized phase 2 study. The primary outcome is Overall Survival.

2. Clinical Question

3. Trial Design

This was a randomized phase II trial with a parallel-group design and no masking. It compared bevacizumab alone with bevacizumab plus radiation therapy in people with recurrent glioblastoma. The registry record lists 182 participants enrolled and the study status as completed. The record describes bevacizumab as given every 2 weeks in both arms; radiation therapy was added in the combination arm.

The primary outcome was overall survival. The registry defines survival time as the interval from randomization to death from any cause or last known follow-up, with participants without a recorded death by their last known follow-up censored in the analysis. The primary outcome description gives 18-month survival rates and says that survival distributions were to be compared between arms. The analysis was planned to occur when 135 deaths were reported. Maximum follow-up at the time of analysis was 52.8 months.

The listed primary analysis population is eligible participants. The primary outcome arm counts are 84 for bevacizumab and 86 for bevacizumab plus radiation therapy. These counts describe the posted analysis and should not be treated as a complete account of enrollment or eligibility. The registry record does not report the detailed eligibility criteria, the original sample-size justification, the planned allocation ratio, or further details about treatment delivery and follow-up procedures.

The study began on 2012-12-20, had primary completion on 2018-09-03, and is recorded as completed. The sponsor was the Radiation Therapy Oncology Group. The registry identifies five secondary outcomes in addition to overall survival: best response, progression-free status at 6 months, progression-free survival, and central nervous system toxicity outcomes at different periods after radiation therapy began.

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: Eligible participants

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: Eligible participants

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival, measured over From randomization to last follow-up. Maximum follow-up at time of analysis was 52.8 months..

Overall survival measures the time from randomization until death from any cause. If death has not been recorded by the last known follow-up, that participant's survival time is censored at that follow-up. This endpoint captures death regardless of its specific cause, rather than focusing only on tumor response or progression.

The registry describes survival rates estimated by the Kaplan–Meier method and reports 18-month rates. In general, Kaplan–Meier estimation uses the observed timing of events while accounting for participants whose follow-up ends before an event is observed. The log-rank method compares the pattern of event times between groups across follow-up, rather than comparing only the proportion of participants alive at one selected time.

Overall survival is often useful in clinical trials because it is a direct time-to-event outcome. It can incorporate the timing of deaths and follow-up that varies among participants. That does not remove the need to consider the length and completeness of follow-up, censoring, and the uncertainty around estimates. In this trial, the reported survival analysis includes a hazard ratio, confidence interval, and log-rank p-value, while the arm-specific 18-month estimates have their own confidence intervals. These quantities answer related but distinct questions: the rates describe estimated survival at a stated time, while the log-rank analysis compares the survival distributions across the recorded follow-up.

7. Results Posted in the Registry

• Bevacizumab + RT: 22.1% (19/86) versus 25.0% (21/84) on control; risk difference -2.9 percentage points (95% CI -15.7 to 9.8), risk ratio 0.88 (0.51–1.52); unadjusted two-proportion z-test p = 0.655.

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.

Percentage of Participants With Complete or Partial Best 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 + RT: 29.9% (23/77) versus 20.5% (16/78) on control; risk difference 9.4 percentage points (95% CI -4.2 to 23.0), risk ratio 1.46 (0.84–2.54); unadjusted two-proportion z-test p = 0.180.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bevacizumab + RT and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Progression-free at 6 Months

• 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 + RT: 54.3% (44/81) versus 29.1% (23/79) on control; risk difference 25.2 percentage points (95% CI 10.4 to 40.0), risk ratio 1.87 (1.25–2.78); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Bevacizumab + RT than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Progression-free Survival

• 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 + RT: 8.1% (7/86) versus 8.3% (7/84) on control; risk difference -0.2 percentage points (95% CI -8.5 to 8.1), risk ratio 0.98 (0.36–2.66); unadjusted two-proportion z-test p = 0.963.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bevacizumab + RT and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover tumor response, progression-free status at a fixed follow-up point, progression-free survival over follow-up, and central nervous system toxicity. Taken together, the posted results are not uniformly aligned in direction or strength. The fixed-time progression-free outcome shows a clearer separation between arms than the response outcome, while the time-to-event progression-free result is more uncertain. This pattern does not establish a consistent benefit across secondary measures.

The primary endpoint remains overall survival, and its reported time-to-event comparison does not show a clear separation between the groups. Differences in secondary endpoints can provide context about response or progression, but they do not replace the primary survival analysis. Each outcome has its own definition, follow-up structure, analysis population, and uncertainty, so patterns across outcomes should be interpreted cautiously.

Unadjusted secondary results carry less evidential weight when several outcomes are examined. In general, testing many outcomes increases the chance that at least one result appears statistically notable even when no corresponding effect exists. Methods that control multiplicity can address that issue, but whether such adjustments were planned or applied is not reported in the registry record. The secondary results are therefore best treated as supportive or exploratory evidence, rather than as independent confirmation of the primary result.

Different denominators across secondary analyses also matter. The recorded outcome counts vary, and the registry record does not explain all reasons for those differences. Such variation can reflect outcome-specific availability or analysis requirements, but its cause should not be assumed in this trial. The record does not report a unified missing-data account for all secondary outcomes.

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

• Percentage of Participants With Complete or Partial Best Response
• Percentage of Participants Progression-free at 6 Months
• Progression-free Survival
• Percentage of Participants With Grade 3+ Central Nervous System (CNS) Toxicity Within 90 Days of Start of Radiation Therapy Reported as Possibly/Probably/Definitely Related to Protocol Treatment
• Number of Participants With Grade 3+ CNS Toxicity More Than 90 Days of Start of Radiation Therapy Reported as Possibly/Probably/Definitely Related to Protocol Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does a Kaplan–Meier estimate describe?

Kaplan–Meier estimation is a method for describing time until an event when participants can have different lengths of follow-up. For this outcome, the event is death from any cause. A participant who is last known to be alive contributes follow-up until that time and is then censored, rather than being counted as having died. The method uses the event and censoring times to estimate survival over follow-up. The registry reports an 18-month survival estimate for each arm, with a 95% confidence interval.

As a general statistical point, censoring is not the same as a death or as proof that a participant remained alive indefinitely. Interpretation relies on the assumptions used for time-to-event analysis, including that censoring does not systematically conceal a different event experience in a way that invalidates the comparison. The registry record does not report a detailed assessment of those assumptions.

What does the log-rank comparison test?

The log-rank method compares the observed timing of events between groups over follow-up. It makes use of the ordering of event times, rather than reducing each participant's experience to whether an event occurred by one selected date. The primary report gives a hazard ratio of 0.98, a 95% confidence interval from 0.70 to 1.38, and p = 0.46. A hazard ratio is a relative summary of event rates over time under the analysis model; it is not an absolute difference in survival percentages and does not directly describe how many months any individual may live.

In general, a confidence interval for a hazard ratio that includes 1 indicates that the data are compatible with no relative difference as well as with effects on either side of that value. The p-value summarizes how unusual the observed comparison would be under the test's null hypothesis, subject to the method's assumptions. Neither statistic establishes that the groups are equivalent. The registry record does not report an equivalence or non-inferiority objective.

How do the recalculated binary comparisons differ?

The separately recalculated risk differences use the posted arm proportions as binary outcomes. A risk difference is the proportion with the outcome in one group minus the proportion in the other group, as defined by the comparison. Its confidence interval describes uncertainty in that absolute contrast. The unadjusted p-value tests a binary-outcome comparison without adjustment for other factors. These calculations do not use the full time-to-event data, and they do not reproduce the Kaplan–Meier and log-rank analysis.

For overall survival, the binary re-calculation is based on the posted 18-month estimates. It is therefore a fixed-time comparison and should not be interpreted as a second estimate of the log-rank hazard ratio. More generally, a binary analysis can be useful for a clearly defined time point, but it may discard information about when events occurred and about follow-up outside that time point.

What does a confidence interval contribute?

A confidence interval gives a range of effect estimates compatible with the observed data under the stated method. It expresses statistical uncertainty, not a range that contains a fixed proportion of individual participant outcomes. Narrower intervals generally indicate more precise estimates; wider intervals indicate that the data leave greater uncertainty about the effect. The interpretation also depends on the analysis model and the data included.

The 95% intervals for the primary survival estimates and hazard ratio are important alongside the point estimates. A point estimate is one value from the data, while its interval makes visible the uncertainty around it. The intervals do not alone determine clinical importance, and the registry record does not define a threshold for a clinically important survival difference.

Why might over-dispersion matter for other outcome types?

As a general concept, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if a model assumes less variability than the data contain, leading to intervals that are too narrow and tests that appear more decisive than warranted. The posted primary outcome is time-to-event, and the registry record does not report an over-dispersion adjustment for it. The registry record also does not provide enough detail to infer whether over-dispersion was assessed for other outcomes.

What is not described about the analysis plan?

The registry record states that the protocol specified comparing failure-time distributions between arms and that the reported analysis used the log-rank method. It also says the planned analysis point was when 135 deaths were reported. Further details of the statistical plan, including covariate adjustment, interim analyses, handling of deviations from the analysis population, and full model specifications, are not reported in the registry record. They should not be inferred from the posted estimates.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. The primary arm-specific 18-month survival estimates are 25.1% and 21.6%, with 95% confidence intervals of 15.2% to 35.0% and 12.1% to 31.1%, respectively. The breadth of these intervals indicates that the underlying survival rates are not estimated with high precision from the posted data.

The sponsor-reported hazard ratio is 0.98, with a 95% confidence interval from 0.70 to 1.38. This interval includes 1 and permits a range of relative effects, so the point estimate should not be treated as exact. The log-rank p-value is 0.46, but a p-value does not measure the size or precision of an effect; the confidence interval is more informative about the range of effects compatible with the analysis.

The unadjusted risk-difference calculation for the posted 18-month proportions has a 95% confidence interval from -0.157 to 0.099. It includes values on both sides of no difference. This is a different estimand and method from the survival-distribution comparison, so its interval should be interpreted as uncertainty in the binary contrast rather than uncertainty in the hazard ratio.

In general, confidence intervals are affected by the amount of information in the data, event frequency, follow-up, and the analysis method. The record reports arm counts and maximum follow-up, but does not report all details needed to assess the influence of censoring or other sources of uncertainty. The reported intervals are therefore central to understanding the limits of what the results establish.

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 sample-size illustrations use the observed effect as a starting point and show planning figures for detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect. They are not the original design calculations for this trial. The registry record does not report the trial's original sample-size justification or design assumptions.

For binary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total numbers of events, following the Schoenfeld approach. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm, or total events for a time-to-event outcome, associated with an 80% chance of detecting the specified effect under those assumptions if that effect were the true one. The 90% power column gives the corresponding planning quantity for a 90% chance. These are planning concepts, not guarantees about the outcome of a future trial.

Smaller effects generally require more information to detect reliably, so the illustrations increase when the assumed effect is reduced. Estimates based on observed effects can be unstable, particularly when the original trial's estimates are imprecise. These figures are planning illustrations, not observed power. Observed power is not an appropriate way to reinterpret the trial's results after the data have been collected; the effect estimates, confidence intervals, and reported tests are more informative about the results.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.250; treatment proportion p₁ = 0.221; average p̄ = 0.235.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6000 = 1.1760.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5997 = 0.5047.
4. n = (1.1760 + 0.5047)² / (-0.0291)² = 3,342.9, rounded up to 3,343 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
p0 <- 0.25                          # control proportion
p1 <- 0.22093023255814                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1730950)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 3,343 (80% power), 4,475 (90% power)
 75% of observed effect: n per arm = 6,007 (80% power), 8,042 (90% power)
 50% of observed effect: n per arm = 13,657 (80% power), 18,283 (90% power)
power.prop.test: 3342.9 
Simulated power at n = 3,343 per arm: 0.807 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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. Analyses Reported by the Sponsor

The registry's own primary analysis is the log-rank comparison of overall survival. It reports a hazard ratio of 0.98, a 95% confidence interval from 0.70 to 1.38, and p = 0.46. That time-to-event analysis is the main reported comparison for the primary endpoint because the endpoint is defined by time from randomization to death or last known follow-up.

The separate recalculation uses the posted arm-level 18-month proportions as a binary comparison. It gives a risk difference of -0.029, a 95% confidence interval from -0.157 to 0.099, and p = 0.655. It does not use the recorded event times in the way the Kaplan–Meier and log-rank methods do. The two analyses therefore should not be expected to yield identical estimates or p-values, and the recalculated risk difference is not a correction of the registry analysis.

The registry record does not flag a discrepancy between the posted results and the recalculation. Even so, the methods answer different statistical questions: one compares survival distributions over follow-up, and the other contrasts binary proportions at the reported time point. For interpretation of the primary endpoint, the registry's own time-to-event analysis takes precedence as the analysis specified in the record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes in addition to overall survival. Testing multiple outcomes creates a multiplicity issue: even if each individual test uses a conventional threshold, the chance of at least one apparently positive result across a collection of tests can increase. In general, prespecified procedures such as family-wise error control or a hierarchical testing strategy can help address this concern. Whether any such procedure was prespecified or used is not reported in the registry record.

The secondary outcome results should therefore be read with their individual confidence intervals and p-values, but without assuming that each unadjusted result independently confirms an effect. The registry reports unadjusted p-values for several comparisons. It does not report a multiplicity-adjusted analysis or explain whether the secondary outcomes were intended to be confirmatory or exploratory.

The primary analysis population is described as eligible participants, and primary arm counts are recorded as 84 and 86. Counts for secondary outcomes differ. The registry record does not give a complete participant flow, explain all differences in denominators, or report detailed missing-data methods such as imputation or sensitivity analyses. The primary endpoint description does state that participants are censored at last known follow-up if no death is recorded. That is a time-to-event convention, not a general account of missing data across all outcomes.

The trial record says that analysis was planned when 135 deaths were reported, but it does not report whether interim analyses occurred or whether any monitoring or stopping boundaries were used. Additional aspects of the statistical analysis plan, including detailed covariate adjustment, prespecified subgroup analyses, and handling of protocol deviations, are not reported in the registry record. Those omissions limit how fully the posted results can be assessed against the intended analysis plan.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: seizure (8.4%), encephalopathy (3.9%), generalized muscle weakness (3.6%), lung infection (2.6%), wound infection (2.6%).

The registry reports serious adverse event information by arm, including the number at risk and the number affected. For bevacizumab, 76 participants were at risk for the serious-event summary and 27 were affected; for bevacizumab plus radiation therapy, 83 were at risk and 29 were affected. The registry also reports other adverse-event counts and deaths: 70 affected among 76 at risk in the bevacizumab arm, and 73 affected among 83 at risk in the combination arm; deaths are listed as 4 and 8, respectively.

The most frequently listed serious terms include seizure at 8.4%, encephalopathy at 3.9%, generalized muscle weakness at 3.6%, lung infection at 2.6%, wound infection at 2.6%, and back pain at 2.6%. These are registry-reported event terms and percentages. They do not, by themselves, establish that an event was caused by treatment. The registry separately describes some central nervous system toxicity outcomes as possibly, probably, or definitely related to protocol treatment, but the listed serious-event summary does not provide enough detail to infer causality or compare event severity comprehensively.

Safety counts should be considered alongside the stated denominators, definitions, and follow-up. More detailed information about event timing, duration, recurrence, and attribution is not reported in the registry record.

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

The primary result is an estimate of overall survival under the two randomized strategies, not a guarantee about any individual participant's outcome. The registry's log-rank comparison reports a hazard ratio of 0.98 with a 95% confidence interval from 0.70 to 1.38 and p = 0.46. This analysis does not establish a clear difference in overall survival between the arms. It also does not establish that the strategies are equivalent, because the interval allows a range of possible relative effects.

The 18-month survival estimates provide a fixed-time view, while the log-rank result compares event-time patterns across follow-up. Their point estimates should not be treated as interchangeable measures. The unadjusted binary re-calculation is also not a substitute for the reported time-to-event analysis. Each statistic has a distinct definition and should be interpreted accordingly.

The secondary outcomes offer additional information about response, progression, and toxicity, but multiple outcomes and differing analysis populations make it important not to elevate an isolated secondary finding above the primary result. Unadjusted secondary findings are especially uncertain when the registry does not describe multiplicity control.

These results do not, on their own, show why any observed difference occurred, establish the mechanism of an outcome, or answer questions about people outside the trial's eligible population. They do not define a clinically important survival difference, and the registry record does not report a threshold for one. The findings describe the data and analyses recorded for this randomized phase II trial; their precision and the analysis details set limits on the conclusions that can be drawn.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of endpoint and analysis matters. Overall survival is a time-to-event outcome, so the registry's Kaplan–Meier estimates and log-rank comparison use information about when deaths occurred and account for participants whose follow-up ends before a recorded death. A binary comparison at a selected time point answers a narrower question and can produce a different estimate and p-value without contradicting the time-to-event analysis.

It also illustrates why a point estimate should be read together with its confidence interval. The primary hazard-ratio estimate is close to 1, but its interval spans a range of plausible relative effects. A non-significant test does not prove there is no effect, and a point estimate alone does not establish that an effect is important. The precision of the evidence is part of the result.

The secondary findings show another statistical issue: several outcomes may be measured in one trial, and a result on one outcome does not automatically confirm the primary hypothesis. Without a reported multiplicity strategy, the strength of unadjusted secondary findings should be weighed cautiously. Differences in outcome denominators also remind readers to check which participants contribute to each estimate.

Finally, planning illustrations based on observed effects can help explain how assumptions about effect size relate to required information, but they are not evidence of the trial's original design rationale or of the probability that its result is true. The original sample-size justification is not reported in the registry record. Keeping planning calculations separate from observed results helps avoid overstating what the trial establishes.

19. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not provide a detailed account of eligibility criteria, participant flow, or all reasons that outcome denominators differ. Although the primary analysis is described as involving eligible participants, the relation between that population and all enrolled participants is not fully documented in the posted results. This limits assessment of how the analysis population was formed.

The study was unmasked, so participants and investigators were not blinded according to the registry entry. The record does not describe whether outcome assessment was blinded or how response and toxicity assessments were standardized. Those details may be relevant to outcomes requiring assessment, but they cannot be inferred from the masking field alone.

The registry reports overall survival rates and a log-rank comparison, but it does not provide all details of the statistical plan, including covariate adjustment, sensitivity analyses, or the handling of protocol deviations. The record states that analysis was planned after 135 deaths, but does not report whether interim analyses took place. The original sample-size rationale and the trial's design assumptions are also not reported.

The secondary outcomes are numerous, and the registry does not report multiplicity adjustment. Missing-data methods beyond censoring for the primary time-to-event outcome are not reported. These omissions limit assessment of the robustness of secondary findings and the effects of incomplete outcome information.

Maximum follow-up at analysis was 52.8 months, but the registry does not give further detail about follow-up completeness or the distribution of follow-up times by arm. Confidence intervals for the primary results are broad. The findings therefore have meaningful statistical uncertainty, and the posted record does not provide a defined threshold for clinical importance.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Bevacizumab With or Without Radiation Therapy in Treating Patients With Recurrent Glioblastoma — NCT01730950.
• Registry record last updated 2022-12-29; status last verified 2022-12.
• Results first posted 2020-03-17.
• 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.

23. Record Summary

NCT01730950 is a completed randomized phase II parallel-group trial sponsored by the Radiation Therapy Oncology Group. It enrolled 182 participants and compared bevacizumab every 2 weeks with the same bevacizumab schedule plus radiation therapy for recurrent glioblastoma. The study began on 2012-12-20, and primary completion was recorded as 2018-09-03.

The primary outcome was overall survival, measured from randomization to death from any cause or last known follow-up. The registry reports 18-month survival estimates and a log-rank comparison. The reported hazard ratio was 0.98, with a 95% confidence interval from 0.70 to 1.38 and p = 0.46. Secondary outcomes addressed response, progression-free status and survival, and central nervous system toxicity.

The posted primary analysis does not establish a clear difference in overall survival between the randomized groups. Its confidence interval allows a range of possible effects, and several details about the original design and analysis plan are not reported in the registry record.