Dasatinib and Bevacizumab in Treating Patients With Recurrent or Progressive High-Grade Glioma or Glioblastoma Multiforme: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dasatinib and Bevacizumab in Treating Patients With Recurrent or Progressive High-Grade Glioma or Glioblastoma Multiforme (NCT00892177), a randomized phase 2 study. The primary outcome is Number of Participants With Dose Limiting Toxicities to Determine Maximum Tolerated Dose (MTD) of Dasatinib in Combination With Bevacizumab (Phase I).

2. Clinical Question

3. Trial Design

The study is listed as a phase II, randomized, double-blind, parallel trial, with a phase I component described as completed. Its title and official title distinguish dose finding from the randomized comparison: phase I assessed dasatinib dose and tolerability with bevacizumab, while phase II compared bevacizumab plus dasatinib with bevacizumab plus placebo. The registry lists an overall enrollment of 144 and a completed status. The start is recorded as 2009-10 and primary completion as 2014-11.

In phase II, participants were assigned to one of two arms. The experimental arm received bevacizumab on Day 1 and dasatinib on days 1-14; the comparator arm received bevacizumab on Day 1 and placebo on days 1-14. Courses were described as repeating every 14 days while disease progression or unacceptable toxicity was absent. The record labels the study randomized and double blind, but details about the allocation procedure, concealment, who was masked, and how masking was maintained are not reported in the registry record.

The primary endpoint concerns phase I rather than the randomized phase II comparison. It counts participants who developed dose-limiting toxicities and uses those observations to determine the maximum tolerated dose. The record reports dose-level results and a maximum tolerated dose of 100 mg. For phase II, posted outcome populations differ by endpoint: overall survival and time to progression each list 83 participants in the dasatinib arm and 38 in the placebo arm, while the adverse-event record gives different at-risk counts. Reasons for these differences and the phase II analysis-population definitions are not reported in the registry record. The record does not explain the phase II sample-size rationale or the planned statistical analysis in sufficient detail to assess those aspects of design.

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.

Phase I: Dose Level 0

Phase I: Dose Level 1

Phase I: Dose Level 2

Phase I: Dose Level 3

Analysis population for the primary outcome, as defined in the registry: Adverse event information is available for 4 patients on study 1 dose level 1 (with 1 being a MTD replacement due to disease progression prior to completing cycles 1 and 2).

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Dose Limiting Toxicities to Determine Maximum Tolerated Dose (MTD) of Dasatinib in Combination With Bevacizumab (Phase I), measured over 14 days.

The designated primary endpoint counts participants who developed dose-limiting toxicities during phase I. It was intended to support selection of the maximum tolerated dose of dasatinib when combined with bevacizumab. Toxicity is assessed over the early treatment period because dose-finding decisions depend on whether participants experience treatment-limiting harms at the dose being evaluated. The registry defines the MTD as the dose at which fewer than one-third of patients experience a DLT, with specified escalation and cohort rules. It describes the dose as the level at which 0/6 or 1/6 patients experience DLT and the next higher dose has at least 2 out of 3 or 2 out of 6 patients with DLT. The record also describes treating three patients at each dose level and adding three more if one DLT occurs.

The endpoint is a count of participants with DLT, not a measure of tumor response, survival, or comparative phase II efficacy. The endpoint description says the assessment is based on DLT during the first 4 weeks, following the first 2 treatment cycles, while the listed timeframe is 14 days. The relationship between those two time descriptions is not explained in the registry record. The record reports 100 mg as the MTD and lists dose-level DLT counts. Those observations describe the phase I dose-finding result; they do not by themselves answer whether adding dasatinib changes phase II outcomes.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Phase I dose finding and phase II comparison use different statistical ideas. The primary endpoint is a toxicity count across dose levels. Phase II overall survival and time to disease progression are time-to-event outcomes, with analyses reported using Kaplan Meier methods and hazard ratios. A count of participants with DLT, a median time, and a hazard ratio answer distinct questions; one cannot substitute for another.

What does the phase I count represent?

The phase I endpoint records how many participants experienced a dose-limiting toxicity at each dose level. The registry’s rule uses these observations to select a maximum tolerated dose, with cohort expansion when a DLT occurs and escalation stopping when the specified toxicity pattern is reached. Such rules are a dose-finding framework: they organize decisions as safety information accumulates across dose levels. The reported MTD is 100 mg. The record does not provide a full dose-to-mg mapping for each listed cohort, nor does it report a separate statistical uncertainty interval for the MTD.

In general, small dose-finding cohorts are designed to guide dose selection rather than estimate uncommon toxicity rates precisely. A count of zero DLTs in a cohort does not establish that the dose has no risk; it describes the observed participants under the endpoint definition. The registry notes a replacement participant at dose level 1 after disease progression before completion of cycles 1 and 2. The reason for that replacement is described, but broader handling rules for participants who do not complete the assessment period are not reported in the registry record.

How should a Kaplan Meier estimate be read?

In general, the Kaplan Meier method estimates the probability of remaining free of an event over time while accounting for participants whose event status is not observed for the entire follow-up period. The median is the time at which the estimated event-free proportion reaches the midpoint, when that point can be estimated. For survival, the event is death; for time to progression, the event is disease progression as defined by the study. The registry reports medians and 95% confidence intervals for the medians, but does not include the detailed endpoint definitions, censoring rules, or follow-up procedures needed to assess those estimates fully.

A hazard ratio compares event rates over follow-up under the model and analysis used. A value of 1 represents equal hazards in the comparison as parameterized; values on either side represent different relative rates. The clinical meaning depends on which arm is in the numerator, the event definition, and whether the model assumptions are reasonable. The posted comparison labels the arms and reports hazard ratios, confidence intervals, and p-values, but details such as model diagnostics and adjustment variables are not reported in the registry record.

What does a confidence interval add?

In general, a confidence interval conveys the uncertainty around an estimated effect under the method’s assumptions. A 95% confidence interval is not a guarantee that the true effect lies in the particular interval. Instead, the confidence level describes the long-run behavior of the interval procedure under repeated use when its assumptions hold. For these phase II comparisons, the reported intervals include 1, so the estimates do not rule out equal hazards. Their ranges also encompass effects in either direction, which means the data do not pin down a narrow comparative effect.

A p-value describes how incompatible the observed data are with a specified null hypothesis under the statistical model. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The p-values reported for the phase II outcomes should be read together with the point estimates, confidence intervals, endpoint definitions, and analysis populations. A p-value alone cannot establish equivalence, prove absence of an effect, or resolve concerns about missing data or multiplicity.

What are the planning illustrations?

The posted planning illustrations are based on the observed effect, not the trial’s own design. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For time-to-event outcomes, the illustrations concern total events using a Schoenfeld approach; for other outcomes, the stated convention is participants per arm. The entries vary the effect to detect as a fraction of the observed effect and give planning requirements for 80% or 90% power. These are hypothetical design calculations, not observed power and not evidence that the completed trial had that power.

In general, a planning calculation answers a conditional question: how much information might be needed under specified assumptions to detect a particular effect. It does not show the probability that a completed study has discovered a true effect, and it cannot repair limited precision in the observed estimates. The actual phase II design assumptions, target effect, sample-size justification, and any planned interim analyses are not reported in the registry record. The illustrations should therefore remain separate from conclusions about the study’s original design or its results.

Over-dispersion is a general concern for count outcomes when observed variability exceeds what a simple count model assumes. It can make standard errors too small if it is ignored. The primary DLT endpoint is presented as dose-level counts, but the registry record does not report a model-based comparison or a dispersion estimate. The phase II time-to-event analyses use a different framework, so count-model concerns should not be imported into their interpretation. More generally, statistical methods need to match the endpoint and the way observations were collected.

10. Analyses Reported by the Sponsor

The registry reports the phase I maximum tolerated dose as 100 mg. This is the sponsor’s recorded dose-finding conclusion and takes precedence over any simple re-calculation from the posted dose-level counts. Reconstructing the dose-escalation decision from counts alone would require the full sequence of dose assignments, timing, and application of the protocol’s cohort rules; those details are not reported in the registry record.

For the randomized phase II outcomes, the record reports Kaplan Meier hazard ratios, confidence intervals, and p-values. The overall-survival comparison is reported as a hazard ratio of 0.92 with a 95% confidence interval from 0.61 to 1.4 and p = 0.7. The time-to-progression comparison is reported as a hazard ratio of 1.14 with a 95% confidence interval from 0.76 to 1.7 and p = 0.52. These are the registry’s own reported analyses; they are not replaced by unadjusted calculations from medians. A hazard ratio cannot generally be reconstructed from two medians alone because the underlying event times and censoring information are needed. No conflicting sponsor analysis is identified in the registry record, and no recalculated estimate should be treated as more authoritative than the reported analysis.

11. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the phase II analyses used a prespecified multiplicity strategy, such as a testing hierarchy or adjustment across outcomes. Several secondary outcome domains are named, including survival, progression, adverse events, quality of life, and objective response. When multiple outcomes are examined, unadjusted p-values can overstate the strength of confirmatory evidence. In general, multiplicity procedures specify how error rates are controlled across tests; without a reported plan, the role of each secondary result in formal inference is unclear.

Missing-data handling and analysis populations are also not reported in sufficient detail. The overall enrollment is 144, while the phase II outcome records list 83 participants for the dasatinib arm and 38 for the placebo arm for the time-to-event analyses. The adverse-event record uses at-risk counts of 84 and 39 for those arms. These values describe different posted analyses; the registry does not explain why the denominators differ, give a participant flow account, or define an intention-to-treat, per-protocol, or other analysis population. It also does not state how incomplete follow-up, withdrawal, or missing endpoint measurements were handled.

In general, missing observations can affect an estimate when the chance that an outcome is unobserved is related to prognosis or treatment. For time-to-event analyses, censoring rules and follow-up completeness are particularly important to interpretation. For quality-of-life outcomes, the timing and handling of unreturned questionnaires matter. The relevant details are not reported in the registry record, so the extent and possible influence of missing information cannot be assessed from the posted summaries alone.

Interim monitoring, stopping rules for the phase II comparison, the statistical analysis plan, and the rationale for the planned sample size are not reported in the registry record. The separate planning illustrations are not evidence of the trial’s original design assumptions. These omissions do not change the reported estimates, but they limit assessment of how the analyses were selected, whether all intended outcomes were reported, and how robust the conclusions are to analysis choices.

12. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hemoglobin decreased (33.3%), fatigue (33.3%), sudden death (33.3%), serum phosphate decreased (33.3%), hypertension (25.0%).

The adverse-event record gives serious-event counts for the phase II arms: 32 of 84 participants at risk in the bevacizumab-plus-dasatinib arm and 18 of 39 at risk in the bevacizumab-plus-placebo arm were affected. Other adverse events are listed for 83 of 84 and 39 of 39 participants, respectively. These are descriptive counts using the registry’s stated at-risk groups; they are not adjusted comparisons, and the different denominators between safety and time-to-event analyses are not explained in the registry record.

The record also lists serious-event terms with percentages, including Hemoglobin decreased, Fatigue, Sudden death, and Serum phosphate decreased at 33.3%, Hypertension at 25.0%, and Diarrhea at 16.7%. The population and denominator behind these term percentages, and whether terms could overlap within participants, are not reported in the registry record. The figures should not be interpreted as comparative treatment effects or as proof that a treatment caused an event. Death counts are not reported in the registry record. The safety summaries describe observed events; they do not by themselves establish the full balance of harms between randomized arms.

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

The phase I result means that the registry reports a maximum tolerated dose of 100 mg under its stated dose-finding approach. The dose-level counts are observations from the phase I cohorts and provide the basis for the recorded selection. They do not establish that the dose is free of toxicity, that all possible toxicities were captured, or that the same dose has the same risk in every participant. The DLT endpoint also does not measure tumor control or survival.

The randomized phase II estimates compare bevacizumab plus dasatinib with bevacizumab plus placebo for overall survival and time to disease progression. Their reported confidence intervals include 1 and allow for relative effects in either direction. The estimates therefore do not precisely determine whether the regimens differ on those outcomes. This is not proof that the regimens are identical, and it is not proof that one is superior. A demonstration of equivalence or noninferiority would require a suitable design and prespecified margins, which are not reported in the registry record.

Statistical uncertainty is only one limit on interpretation. The registry does not give enough information about analysis populations, missing data, multiplicity, interim monitoring, or the phase II statistical plan to assess those features. The phase II outcome populations are smaller than overall enrollment, and the reasons are not reported. The posted results also do not include detailed numerical findings for every named secondary outcome. Those gaps mean that the available results should not be generalized beyond the reported endpoints and populations.

In general, a clinical trial estimate is evidence about the participants and outcomes analyzed under the study’s methods. It is not a guarantee about an individual’s outcome, nor does a nonsignificant test establish no effect. The record supports describing the reported dose-finding result and the uncertainty in the two phase II comparisons. It does not support a broader claim about all efficacy outcomes, all safety outcomes, or clinical decisions.

14. Why This Trial Matters Statistically

This trial is statistically distinctive because its registry record combines a dose-finding question with a randomized comparison. The primary endpoint belongs to phase I and counts dose-limiting toxicities to select a maximum tolerated dose. The phase II outcomes instead compare time-to-event results between two randomized regimens. Keeping these questions separate prevents a dose-selection result from being misread as evidence about comparative efficacy.

The design also illustrates why endpoint-specific methods matter. Dose-level toxicity counts are interpreted through escalation rules, while survival and progression use Kaplan Meier estimates and hazard ratios. A median describes a time point in an estimated event-time distribution; a hazard ratio compares event rates over follow-up. Neither should be reconstructed from the other without the underlying data and analysis assumptions. The confidence intervals are therefore central to understanding how precisely the phase II comparisons are estimated.

Another statistical lesson is the distinction between a reported result and a planning calculation. The registry’s sample-size illustrations use observed effects and specified assumptions, but they are not the trial’s original design rationale and do not represent observed power. Likewise, unadjusted secondary findings should be interpreted cautiously when several outcome domains are examined and the multiplicity plan is not reported.

Finally, the record exposes the importance of transparent analysis populations and follow-up information. The overall enrollment, time-to-event denominators, and safety at-risk counts are not identical, and the reasons are not explained. Such distinctions are essential for judging how broadly results apply and whether missing outcome information could matter. Statistical interpretation depends not only on estimates and p-values, but also on a clear account of who was analyzed, which outcomes were planned, and how incomplete observations were handled.

15. 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.

A central limitation is that the registry’s designated primary endpoint is phase I dose finding, while the randomized phase II question is represented by secondary outcomes. Readers seeking a primary phase II efficacy result cannot treat the phase I MTD as a substitute. The record names several phase II outcomes, but detailed numerical results are not reported for every named outcome. This restricts assessment of the totality of the randomized evidence.

The number of participants differs across posted summaries. Overall enrollment is 144; the time-to-event arms list 83 and 38 participants, and the phase II safety groups list 84 and 39 at risk. The registry does not explain these differences or give a complete participant disposition. Nor does it report detailed missing-data methods, censoring rules, endpoint definitions for progression, or the analysis population. As a result, the influence of exclusions, incomplete follow-up, and differences in available outcome data cannot be judged.

The record does not report the phase II sample-size rationale, planned effect, analysis plan, interim analyses, or multiplicity procedures. Planning illustrations based on observed effects cannot fill those gaps. The dose-finding endpoint description also gives a timeframe of 14 days while describing DLT assessment over the first 4 weeks after the first 2 treatment cycles; that timing relationship is not clarified. In addition, the serious-event term percentages lack a reported denominator and attribution by randomized arm.

These limitations do not negate the posted estimates, but they constrain how fully the design and analyses can be evaluated. The confidence intervals and p-values should be interpreted as reported, alongside uncertainty about populations, methods, and unreported outcome details. No inference should be made about unreported endpoints or undocumented analysis choices.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Dasatinib and Bevacizumab in Treating Patients With Recurrent or Progressive High-Grade Glioma or Glioblastoma Multiforme — NCT00892177.
• Registry record last updated 2019-10-21; status last verified 2019-10.
• Results first posted 2017-06-27.
• 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.

19. Record Summary

The registry describes a completed randomized, double-blind, parallel phase II study with a phase I dose-finding component. The overall enrollment is 144. Phase I evaluated dasatinib with bevacizumab using dose-limiting toxicities to determine the maximum tolerated dose; the recorded MTD is 100 mg. Phase II compared bevacizumab plus dasatinib with bevacizumab plus placebo.

The posted phase II analyses report overall survival and time to disease progression using Kaplan Meier methods. Both comparisons have confidence intervals that include 1, and the registry does not report a multiplicity plan or detailed analysis-population and missing-data methods. Safety counts are available, but the reasons for differing denominators and the denominator behind serious-event term percentages are not reported. Numerical findings for all named secondary outcomes are not reported in the registry record. The results support a description of the dose-finding outcome and the uncertainty in the posted time-to-event comparisons, with important limits on broader interpretation.