Biostatistical benchmarking of neuro-oncology trials

Abstract

Purpose

High-grade gliomas are among the most treatment-resistant cancers, with few therapies improving survival despite hundreds of clinical trials. The biostatistical parameters used to design these trials are critical but uncharacterized in aggregate. Currently, no data-driven benchmarks exist to inform these parameters, including the target effect size. This study therefore aimed to analyze trends in their use across neuro-oncology trials.

Methods

We systematically searched PubMed for publications of phase 2 and 3 high-grade glioma or medulloblastoma trials comparing two or more arms with a time-to-event primary endpoint. Key biostatistical parameters were extracted from each study, including trial phase, endpoints, effect size, control arm survival assumptions, Type I error, power, sample size, and accrual time.

Results

We analyzed 210 trials published between 1976 and 2025, evaluating 254 primary time-to-event endpoints (overall, OS, or progression-free survival or similar). Survival assumptions and target effect sizes (ie, hazard ratios, HRs) used for trial powering varied substantially. Assumed control arm OS was often lower than observed OS, and the application of type I error rates did not consistently reflect the stated hypothesis directionality. Trials with planned sample sizes below 500 and lower HR targets were less likely to meet accrual goals. Trials generally aimed to complete accrual by 36 months with a median follow up of 24 months.

Conclusion

This study provides historical benchmarks for sample size assumptions to support more transparent, data-driven, and context-aware trial design. They may also serve as a resource for feasibility planning, protocol development, and statistical justification in future trials.

Key Points.

• Biostatistical assumptions vary across neuro-oncology clinical trials.

• Treatment effect and control arm survival are often mis-specified during trial planning.

• Benchmarks provided here can guide trial design, justification, and feasibility.

IMPORTANCE OF THE STUDY

By systematically analyzing long-overlooked biostatistical assumptions and parameters across 210 neuro-oncology trials, this study provides the first systematic, quantitative benchmarks for the biostatistical parameters used to power neuro-oncology trials. These benchmarks are not intended to be prescriptive but to serve as general reference points that support design transparency, justification, and modeling. They may guide expectations regarding clinical benefit (eg, target effect size) and support protocol justification to key stakeholders, including trial sponsors, patient groups, and regulatory bodies. Additionally, they may be valuable for trial modeling efforts, such as informing Bayesian priors and simulation-based designs. Ultimately, we hope these benchmarks will promote more transparent and context-aware trial design.

Introduction

High-grade gliomas (HGG) are among the most treatment-resistant human cancers. Despite decades of clinical research, few therapies have improved outcomes for patients with glioblastoma (GBM), the most common HGG. Of the hundreds of therapeutic clinical trials in GBM,¹ only three treatments—radiation therapy,² temozolomide,³ and tumor-treating fields4—have demonstrated survival benefit in a phase 3 randomized clinical trial (RCT) and been adopted as standard of care. Surgical resection remains a mainstay of care,⁵ albeit unsupported by RCT evidence—the gold standard for evaluating treatment efficacy in most clinical settings.

This limited progress has prompted calls from expert groups to improve HGG trial designs.^6–23 For example, in 2020, the Society for Neuro-Oncology encouraged the greater use of prospective, two-arm RCTs with time-to-event endpoints, such as progression-free (PFS) or overall (OS) survival, even in early-phase studies.⁶ Building on these foundational recommendations, guidance on the underlying biostatistical assumptions required to design such trials remains lacking.

No data-driven benchmarks currently exist to inform the quantitative assumptions critical to neuro-oncology trial designs, especially the target effect size. Most existing guidance addresses general trial methodology or conduct, not the quantitative biostatistical parameters that shape trial feasibility, statistical power, and interpretability. (A recent report focused on subgroup analyses.²²)

To address this gap, we reviewed published multi-arm neuro-oncology trial results and protocols to survey the biostatistical parameters commonly used in their design. Our findings provide data-driven, historically grounded benchmarks to inform neuro-oncology trial design.

Methods

We systematically searched PubMed for English-language publications through October 15, 2025, to identify phase 2 and phase 3 clinical trials in gliomas or medulloblastoma comparing two or more arms using a primary endpoint that can be collected as time-to-event, such as OS or a variation of PFS, including event-free survival, time-to-treatment failure, or objective response (if reported as time-to-event). An experienced health sciences librarian (GG), in collaboration with two co-authors (RK and AM), developed the search strategy: (Glioma [MeSH] OR glio*[tiab] OR astrocytoma*[tiab] OR oligodendroglioma*[tiab] OR medulloblastoma*[tiab] OR ependymoma*[tiab]) AND trial[tiab]. Publications describing trial protocols were included if final results were not yet available. Secondary publications reporting only long-term follow-up were excluded, as most trials are not initially powered for the long-term follow-up. Bayesian-designed trials were excluded because they employ fundamentally different analytic frameworks, including dynamic priors, posterior probabilities, and interim adaptations that are not directly comparable to frequentist design parameters, which are more familiar. Additionally, many Bayesian trials do not report power or fixed Type I error rates in a manner compatible with our extraction framework. Basket trials were similarly excluded.

Supplemental Figure 1 outlines the quantitative flow of the article review process, including PubMed and ClinicalTrials.gov searches. After removal of duplicates, titles and abstracts of unique records were screened by five co-authors (LL, RK, GG, BS, and AM) independently, leading to the inclusion of 210 records from which data were extracted. Discrepancies in study eligibility and data extraction were resolved by consensus between RK and AM.

From each eligible publication, we extracted the year of publication, trial phase, primary endpoint(s), hypothesis type (superiority, non-superiority, inferiority, non-inferiority, or equivalence), tumor diagnosis (see Supplemental Figure 2), and biostatistical parameters used for sample size determination. If the publication or its appendix did not contain sufficient information about their biostatistical assumptions, bibliography and/or clinicaltrials.gov was searched for the full study protocol. Biostatistical parameters included the planned effect size, type I error and its sidedness, statistical power, accrual duration, planned follow-up, and final calculated sample size. We also recorded the final sample size achieved and the final observed effect size. To ensure consistency, all effect sizes were expressed as HRs. If not reported, HRs were estimated using the ratio of median survival times (when available), or by calculating log(A)/log(B), where A and B represent survival probabilities at a given time point in each group, under the assumptions of constant hazards (exponential distribution) and proportional hazards.

Descriptive statistics, two-group comparisons, and linear regression analyses were performed using R (version 4.2.0). Non-parametric methods (eg, Wilcoxon rank-sum test for unpaired data and Wilcoxon signed-rank test for paired data) were used unless otherwise specified. For categorical or binary variables, comparisons were performed using Fisher’s exact test or Chi-square test, as appropriate. Linear regression was applied to assess correlations among continuous variables. Correlation was quantified using Pearson’s correlation coefficient, r. Statistical significance was defined as a two-sided P value <0.05. Data plots were generated using the ggplot2 package.

Results

Trial Characteristics

We reviewed 210 clinical trials involving patients with glioma or medulloblastoma, published between 1976 and 2025 (median publication year: 2015; Table 1; Supplemental Figure 3). Although only 31 trials (14.8%) were published before the year 2000, we included them to enable broader and more longitudinal assessments of biostatistical design trends over time. Their inclusion supports the characterization of temporal shifts in trial methodology, such as evolving assumptions around control arm survival and hypothesis testing. A majority of the trials (n > 190, >90.4%) included patients with HGG, of which 124 (59%) enrolled only GBM patients—81 newly diagnosed, 40 recurrent, and three newly diagnosed or recurrent GBM. Across all trials included, 254 primary or co-primary time-to-event endpoints were evaluated. Most endpoints (n = 193, 76%) were evaluated in newly diagnosed tumors, and 56 (22%) in recurrent or progressive tumors. A total of 132 endpoints (52%) were evaluated in phase 3 trials, 111 (43.7%) in phase 2 trials, and 11 (4.3%) in phase 2/3 trials. OS was more commonly used as an endpoint (n = 165, 65%) than PFS or its variations (n = 89, 35%) across all phases (99 vs 33 in phase 3, 8 vs 3 in phase 2/3, and 58 vs 53 in phase 2; Fisher’s Exact P < 0.001).

Table 1.

Description of the 210 trials testing 254 primary endpoints

Characteristic	Value
Year (range, median [interquartile])	1976–2025, median 2015 [2004–2021]
Diagnoses
Newly diagnosed tumors
Glioblastoma	81
High-grade glioma	40
Low-grade glioma	9
Anaplastic glioma	8
1p/19q-codeleted glioma	5
Medulloblastoma	4
Anaplastic astrocytoma	4
Pontine glioma	4
Ependymoma	1
Recurrent tumors
Glioblastoma	40
High-grade glioma	8
Anaplastic astrocytoma	1
New or recurrent tumors
Glioblastoma	3
High-grade glioma	1
Medulloblastoma	1
Endpoints
Overall survival	165
Progress-free survival or similar	89
Phase of endpoints
2	111
2/3	11
3	132
Endpoint hypothesis
Superiority	241
Non-inferiority	11
Equivalence	2
Number of comparisons in each trial
One	174
Two	28
Three	8
Missing information
Effect size	81
Type 1 error	55
Type 1 error sidedness	84
Power	72
Predetermined sample size	40

Most endpoints were tested using a superiority hypothesis (n = 241, 94.9%), followed by non-inferiority (n = 11, 4.3%) and equivalence (n = 2, 0.8%). Trials of elderly brain tumor patients had a high proportion of endpoints tested with a hypothesis other than superiority. A total of 12 endpoints (11 OS, 1 PFS) were compared across 11 trials of elderly patients with newly diagnosed GBM (n = 9) or HGG (n = 2). Of these 12 endpoints, 8 (66.7%) underwent superiority, 3 (25%) underwent non-inferiority, and 1 underwent equivalence hypothesis testing (Fisher’s Exact P = 0.002, compared to proportions of different hypotheses tested in non-elderly patients).

Type I Error and Power

The most commonly accepted type I error (false positive) rates for powering these trials were 10%, 5%, and 2.5%, with 5% serving as both the median and mode (Figure 1A). Phase 3 trials generally used lower type I error thresholds than phase 2 trials (P ≤ 0.002; Figure 1A), consistent with the conventional practice of allowing more leniency in type I error at earlier trial phases. Although nearly all trials employed unidirectional hypotheses (ie, superior or non-inferiority), 105 endpoints (41.3%) were tested using two-sided type I error rates. The sidedness was not specified for 84 endpoints (33.1%). Excluding the latter, the sidedness of type I error did not differ by trial phase (Fisher’s exact P = 0.08). However, one-sided type I error rates were nominally higher than two-sided error rates in PFS endpoints (P < 0.001; Figure 1B). This difference aligns with statistical expectations: a one-sided type I error of 5% is comparable to a two-sided error of 10% under standard power and sample size assumptions, keeping all other parameters constant. However, this expected relationship between sidedness and type I error was not statistically evident for OS endpoints (P = 0.3). Most trials were powered at either 80% or 90%, with 80% being the median and mode (Figure 1C).

Figure 1.

Distributions of type I and II errors by endpoint and trial phase. (A) Accepted type I error rates, (B) sidedness of type I error, and (C) type II error rates (represented as statistical power) for overall (OS) and progression-free (PFS) survival outcomes. Boxplots show the median and interquartile range.

Expected Control Arm Survival

Estimating survival in the control arm is essential for determining statistical power. Diagnosis-specific distributions of the expected median OS and PFS in control arms are shown in Figure 2A and B. For instance, among trials enrolling patients with newly diagnosed GBM without specifying MGMT promoter methylation status, the expected median OS ranged from 5.75 to 17 months, with a median of 14 months (IQR 11–14.8). Across most diagnoses, expected OS was generally underestimated (Figure 2C), whereas PFS estimates were more aligned with observed values (Figure 2D). This disconnect between clinical outcomes and trial design expectations was statistically significant when comparing paired values of expected versus observed OS in newly diagnosed GBM trials (P = 0.02) and across all trials (P = 0.001).

Figure 2.

Expected and final (observed) control arm survival. (A and B) Expected median overall (OS) and progression-free (PFS) survivals in control arms. Data from diagnosis with a single trial are not shown. (C and D) Difference between expected and final observed median OS and PFS, respectively; negative values indicate underestimation. (E and F) Scatter plots of final and expected control arm median OS over time in newly diagnosed GBM trials. Red lines depict linear regression fits; shaded bands represent 95% confidence intervals. Horizontal bar plots adjacent to figures indicate the number of trials represented. Abbreviations: 1p/19q-codel = diffuse glioma with 1p/19q codeletion; AA = anaplastic astrocytoma; G3G = grade 3 diffuse glioma; GBM = glioblastoma; HGG = high-grade (grade 3 or 4) diffuse glioma; mMGMT = MGMT promoter methylation; umMGMT = MGMT promoter unmethylation; See Supplemental Figure 2 for hierarchical relationships among these categories of diagnoses.

In newly diagnosed GBM trials, median OS observed in control arms increased over time—by approximately 0.29 months (or ∼1.25 week) per year (P = 0.002; Figure 2E); on the other hand, the expected OS values used to power these trials remained unchanged (Figure 2F). In a joint regression model with an interaction term for year, the difference in slopes between expected and observed OS was not statistically significant (interaction P = 0.34), but the direction of effects supports our finding of underestimation in design assumptions (Figure 2E and F).

Target Effect Sizes (HRs)

Next, we examined the HRs that trials were powered to detect between the intervention and control arms. We stratified the target HRs based on diagnosis, and when possible, based on subgroups within a diagnosis. For example, for phase 3 newly diagnosed GBM trials, the target HR for 28 OS endpoints that prespecified it ranged from 0.5575 to 0.8239, with a median of 0.6845 (IQR 0.6651–0.75; Figure 3A). There were only 2 non-inferiority (targeting HRs less than 1.61 and 1.32; or 0.62 or 0.76, as inverses for interpretive consistency with superiority HRs) and 1 equivalence (targeting HR of 0.66) OS endpoints across three phase 3 trials (all of elderly GBM patients) with a prespecified target HR that were included. Their exclusion did not significantly change the median target HR of only superiority hypothesis endpoints, which was 0.699 (IQR 0.667–0.75). Target HR for 11 PFS endpoints in phase 3 newly diagnosed GBM trials (which were all superiority) ranged from 0.5279 to 0.78, with a median of 0.67 (IQR 0.605-0.725; Figure 3B), and did not differ from target HR distribution for OS endpoints (P = 0.42).

Figure 3.

Target hazard ratios (HRs) used for trial powering. (A–D) Target HRs for overall (OS) and progression-free (PFS) survivals used in phase 3 and phase 2 trials, respectively. For the few non-inferiority trials, their non-inferiority margins (HR > 1) were inversed before plotting for interpretive consistency with the vast majority of superiority trials. Vertical dashed lines (0.66 and 0.75) provide reference to target HRs for OS in newly diagnosed GBM trials. Data from diagnosis with a single trial are not shown. (E–F) Temporal trends in target HRs for OS and PFS in newly diagnosed GBM trials. Colored lines show regression fits with shaded 95% confidence intervals. Grey background shading in (E) highlights empirical HR variability for visual assessment only. Horizontal bar plots indicate the number of intervention arms analyzed. Abbreviations: 1p/19q-codel = diffuse glioma with 1p/19q codeletion; AA = anaplastic astrocytoma; G3G = grade 3 diffuse glioma; GBM = glioblastoma; HGG = high-grade (grade 3 or 4) diffuse glioma; LGG = low-grade (grade 2) diffuse glioma; MB = medulloblastoma; mMGMT = MGMT promoter methylation; umMGMT = MGMT promoter unmethylation; See Supplemental Figure 2 for hierarchical relationships among these categories of diagnoses.

Figure 3C and D show target HR distributions for OS and PFS endpoints, respectively, for phase 2 trials. Target HR distribution in phase 3 trials of newly diagnosed GBM patients were higher than phase 2, as expected (for OS endpoints: P = 0.056; for PFS endpoints: P = 0.01). The same trend was observed for recurrent GBM for OS endpoints but was not significant (P = 0.09). Within other diagnoses, there were generally no statistically significant differences in target HRs for OS and PFS endpoints between phase 2 and 3 trials.

Figure 3A–D also show the distribution of target HRs in newly diagnosed GBM trials stratified by MGMT promoter methylation status, which did not differ significantly from trials including all GBM patients regardless of MGMT status; however, the number of stratified trials was limited. Another common subgroup comprised elderly patients with newly diagnosed GBM (irrespective of MGMT status), represented in eight phase 3 trials evaluating eight OS endpoints—four of which tested for superiority. Target HRs in this subgroup ranged from 0.59 to 0.7576, with a median of 0.699 (IQR 0.6407–0.7245), and were not significantly different from those in the broader newly diagnosed GBM population. Restricting to the four with superiority hypothesis yielded a median target HR of 0.699 (0.6717–0.7117) and thus did not significantly change the range.

In newly diagnosed GBM trials, although we did not identify a significant change in target HRs for OS over time, we observed an increase in the variability over time (Figure 3E). In contrast, target HRs for PFS decreased over time, although this trend was not significant (P = 0.07; Figure 3F).

Use of Survival Rates

A few trials were powered using survival rates. The time points used for prespecifying in design or reporting results using survival rates ranged from 6 to 60 months for OS and PFS endpoints. Owing to the considerable heterogeneity, we limited our analysis to time points used to power at least three trials per diagnosis. For instance, six endpoints in newly diagnosed GBM trials were powered using 12-month OS rates ranging from 10% to 67.3% (Supplemental Figure 4A). Similar variability in the observed rates was seen, too. PFS-based survival rates also showed similar variability (Supplemental Figure 4B).

Sample Size and Result Precision

Sample size is inversely related to the target HR a trial is powered to detect, as illustrated by the correlation between target HR and dot color in Figure 4. When we examined the relationship between planned sample size and the HR observed in final trial results, we found that smaller trials showed greater variability in observed HRs, whereas this variability narrowed with increasing sample size (Figure 4), suggesting that larger trials yield more consistent and reproducible outcomes.

Figure 4.

Relationship between sample size and result precision. Scatter plot of final sample size and final observed HR across trials. Dot color represents the target HR the trial was powered to detect. For the few non-inferiority trials, their non-inferiority margins (HR > 1) were inversed before plotting the color for interpretive consistency with the vast majority of superiority trials. Grey dots indicate missing data. The grey shaded area illustrates the empirical variability in observed HRs for visual assessment only. Dashed horizontal line marks HR = 1.0.

Trial Feasibility

We evaluated whether planned sample size affected the likelihood of achieving enrollment targets. Predetermined sample sizes were missing or unreported in the final result publication of 40 (19%) trials. Hence, this analysis was conducted using 147 trials that reported the predetermined sample size and had results with the final sample size achieved. Fifty-five (37.4%) trials did not achieve their planned sample size, which we defined as a shortfall of at least two participants or 2%. All had target enrollments at or below 500 and lower target HRs, while trials with planned sample sizes above 500—using higher target HRs—met their accrual goals (Figure 5A and B). About half of the trials (28 of 55; 50.9%) failed to meet their predetermined sample size due to slow accrual or withdrawal of resources (n = 15) or post-randomization exclusion of patients (n = 8), suggesting logistical, operational, or design-related reasons (Figure 5B). In the remaining trials (27 of 55; 49.1%), enrollment shortfalls were attributable to factors such as faster-than-expected event rates, interim analyses, or external trial results indicating futility, efficacy, safety, or ethical concerns. No reason was provided for five trials, two of which had deviations less than ∼1% from their enrollment targets.

Figure 5.

Feasibility and accrual in neuro-oncology trials. (A) Planned versus final sample size per trial. Dots are colored by target HR. For the few non-inferiority trials, their non-inferiority margins (HR > 1) were inversed before plotting the color for interpretive consistency with the vast majority of superiority trials. Grey indicates missing target HR data. The dashed line represents the line of equality (1:1). (B) Same plot as (A), but colored by reported reason for under-enrollment. (C) Relationship between sample size achieved and estimated monthly enrollment rate. (D) Relationship between sample size achieved and reported follow-up duration. Blue lines in (C and D) show regression fits; shaded areas represent 95% confidence intervals.

Enrollment and Follow-up Lengths

We evaluated enrollment and follow-up durations to guide expectations for trial timelines. The median enrollment time was 37 months across all trials and 36 months for newly diagnosed GBM trials. Because the trial infrastructure (for example, number of participating centers) can influence total enrollment time, we analyzed monthly enrollment rate—defined as average participants enrolled per month across all sites—as a center-independent metric. Monthly enrollment rate was positively correlated with final sample size achieved (Figure 5C; P < 0.001; R² = 0.71), suggesting that larger trials accrued participants more efficiently. The average monthly enrollment was 0.031 * final sample size achieved. Given the high R² value, this rate also reflects that most trials aimed to complete enrollment (accrual) by 36 months (1/0.03) or 3 years. This benchmark—though not fully adjusted for variables like total trial duration, number of sites, or site startup time—offers a practical, generalizable metric for feasibility planning in future trials. Follow-up duration also showed no correlation with final sample size achieved (P = 0.9; Figure 5D) or enrollment rate (P = 0.52) and varied widely; the median and most frequent follow-up time was 24 months across all trials and for newly diagnosed GBM trials.

Discussion

This study provides the first empirical survey of biostatistical design parameters across neuro-oncology clinical trials. Despite the central role these parameters play in powering and designing trials, they remain unstandardized and underreported. While a substantial proportion of trials did not clearly report their biostatistical assumptions, several noteworthy trends and patterns emerged among those that did.

Endpoint Selection

Although the use of PFS was higher in phase 2 trials, OS was the most commonly used endpoint across all trial phases, highlighting low reliance on PFS as an endpoint in among neuro-oncology trialists. If used in early-phase trials, it is critical to validate assumptions behind PFS or PFS-like endpoints to be surrogates for OS, which often becomes the definitive endpoint in phase 3 trials, because the surrogacy of PFS or PFS-like endpoints for OS remains uncertain.^9,24,25 Careful justification of endpoints in early-phase trials based on biological relevance, causal pathway, and OS correlation is essential to test therapies with a higher success rate.

Hypothesis Testing Misalignments

Nearly all trials tested superiority hypotheses, reflecting a persistent optimism that new therapies will outperform standard of care. Yet in GBM—a disease with consistently low trial success rates—this design preference may be unrealistic. Testing a non-superiority or futility hypothesis can be efficient in conditions with high trial failure rates.^26,27 Scenarios where equivalence or non-inferiority design trials would be appropriate, such as when evaluating interventions with lower toxicity or improved quality of life, remain underutilized, too.

Notably, trials enrolling elderly patients with newly diagnosed GBM or HGG were less likely to use superiority hypotheses, perhaps reflecting a context-sensitive design approach in this subgroup. Elderly-focused trials exemplify how statistical strategies can be adapted to patient context. For instance, non-inferiority designs may be more appropriate when prioritizing tolerability, and pragmatic endpoints can capture quality-of-life outcomes that are especially relevant in this population. These context-sensitive approaches provide a useful model for tailoring trial assumptions and hypotheses to the characteristics of specific subgroups.

We also observed misalignment between hypothesis directionality and statistical implementation: over 40% of endpoints were tested using two-sided type I error rates despite specifying a unidirectional (ie, superiority) hypothesis. Unnecessarily using a two-sided test for testing a superiority hypothesis potentially wastes resources by requiring larger sample sizes to achieve the same detectable effect (Figure 6A). While our analysis highlights this inconsistency, it is important to note that one-sided tests are designed to detect benefit and do not formally evaluate the possibility of harm. As such, their use must be accompanied by complementary safety monitoring mechanisms—such as interim analyses, DSMB oversight, and predefined stopping rules—that explicitly account for potential adverse outcomes. Incorporating these safeguards ensures that one-sided testing does not compromise patient safety. OS endpoints, in particular, showed inconsistent application of sidedness, with some trials applying one- or two-sided tests interchangeably while maintaining the same nominal significance threshold. All else being equal, inconsistent application of test sidedness can introduce variability in statistical power and reduce efficiency, complicating cross-trial interpretation. Therefore, trialists should explicitly justify the choice of sidedness and ensure that it is aligned with the study hypothesis.

Figure 6.

Impact of ambitious biostatistical parameters in designing a hypothetical phase 3 trial for newly diagnosed GBM. Based on historical benchmarks summarized in this work, a hypothetical trial is crafted as a two-arm, equal allocation (1:1) design with an α of 0.05 and 80% target power, to be completed in five years (three years of uniform accrual and two years of follow-up). Assume that the sample size need not be increased for additional considerations such as drop-outs, loss to follow-up, non-adherence or cross-over, interim analyses, or missing data. (A) Required total sample size as a function of the target hazard ratio under two possible control arm median survivals (16 vs 21 months) and one-sided or two-sided (dotted lines) α of 0.05. These values correspond to the median survival observed without and with tumor-treating fields in the phase 3 trial,⁴ assuming similar rates of MGMT promoter methylation and therapy (ie, extent of resection and chemoradiation completion). Because adoption of tumor-treating fields is variable in practice, the true control arm median survival would likely fall between these two values, discounting the influence of other non-standard-of-care therapies. (B and C) Impact of underestimating the true hazard ratio. When targeting a more ambitious hazard ratio than is true (assumed here to be 0.80, which is the average of the effect sizes seen in temozolomide and tumor-treating fields phase 3 trials), the observed power decreases drastically (B). If maintaining 80% power is required, the necessary one-sided type I error increases (C). Between assuming a control arm median survival of 16 and 21 months, there is only a minor difference in power loss or type I error inflation. (D and E) Impact of underestimating the control arm median survival. When the design assumes a median survival of 16 months in the control arm and a higher control arm survival is observed, observed power decreases (D) by roughly 1% for each month of underestimation (up to 5 months, representing a median survival of 21 months). If 80% power is assumed, then the necessary type I error increases (E), though not at the same rate as the loss of power. Between targeting a hazard ratio of 0.67 and 0.75, there is only a minor difference in power loss or type I error inflation. The dashed diagonal lines depict 1:1 inverse relationship between power and months.

Type I Error and Trial Phase

The result that phase 3 trials generally used lower type I error thresholds than phase 2 trials is consistent with conventional distinctions between trial phases. However, this does not mean that phase 2 trials should always employ higher type I error thresholds. For example, when a phase 2 trial is primarily designed for safety evaluation, type I error should be—and is often—constrained at levels similar to phase 3 trials for ethical reasons, since relaxing error thresholds when assessing safety could expose patients to undue risk.

Expected Control Arm Survival and Target Effect Size

Trials frequently underestimated control arm OS. Furthermore, newly diagnosed GBM trials often assumed more favorable target HRs than those achieved by the only two modern therapies that have demonstrated an OS benefit in phase 3 RCTs: temozolomide³ (HR = 0.828; based on median OS of 12.1 vs 14.6 months in its two arms) and tumor-treating fields⁴ (HR = 0.766; 16 vs 20.9 months in its two arms). These reference effect sizes suggest that many trials were powered to detect benefits exceeding these proven, widely adopted therapies, and thus may have been significantly underpowered (Figure 6B and C). Another noteworthy trend was that the target HRs decreased over time for PFS and PFS-like endpoints in early-phase trials of newly diagnosed GBM patients. If continued, this trend may either compromise the chance to detect at least a modest therapeutic effect or perpetuate the failure rate of phase 3 trials with false-positive results.

The target HR or control arm median OS ranges generated in this work is not prescriptive but references that should be applied with context. For example, setting a target HR of 0.67 (ie, 50% increase in the median survival) or underestimating the control arm median OS reduces sample size requirements but represents an overly optimistic assumption that risks substantial underpowering (ie, falsely negative) or inflation of type I error (ie, falsely positive) in trials (Figure 6D and E). Conversely, targeting an HR closer to 1 (eg, >0.80) requires larger and thus sometimes infeasible trials, but may better align with effect sizes achieved in proven therapies or what stakeholders consider a minimal clinically important effect. The investigators must balance trial feasibility against statistical rigor.

Of note, while the statistical cost of underestimating control arm median OS is smaller and can be mitigated by dynamically updating assumptions using recent trial data or disease-specific registries, mis-specifying the target HR carries far greater statistical penalty (Figure 6B–E).

Although there were limited non-inferiority or equivalence trials, their target HRs were typical of superiority designs. Generally, non-inferiority or equivalence trials adopt margins closer to 1 and necessitate larger sample sizes.

Sample Size, Reproducibility, and Feasibility

Sample size strongly influenced the variability of trial results. Smaller trials exhibited greater dispersion in the final observed effect sizes, while larger trials yielded more consistent estimates. This finding reinforces the importance of adequately powered studies not only for effect detection but also for scientific reproducibility.

We found that smaller trials—often those with lower target effect sizes—were more likely to fall short of their planned sample size due to post-randomization exclusions, slow accrual, or support withdrawal. In contrast, larger trials (sample size >500), which typically employed higher target effect sizes, more reliably met their accrual goals. This highlights the importance of careful realistic planning, operational readiness, and sustained support to ensure successful trial completion, which a consortium or network-support effort commonly provides.

The monthly enrollment rate benchmark should be interpreted cautiously. While most trials in our dataset planned for accrual completion within approximately 36 months, the feasibility of this target depends on trial infrastructure, including whether the study is single- versus multi-center and industry-sponsored versus cooperative group-led.

Limitations

This study has several important limitations. First, caution is warranted in interpreting this study as suggesting that biostatistical parameters can be meaningfully compared across trials, as these parameters are not necessarily derived from the same underlying population—even within a single diagnosis. It may be impractical to expect uniform trial parameters, given that design decisions may also be shaped by local constraints such as funding, accrual feasibility, and institutional or consortium capacity, as well as by prior, well-founded knowledge of specific patient subgroups or anticipated treatment effects. These context-dependent factors (such as number of sites, sponsor type, network/consortiums support, participant drop-out rate, or geographic scope) are not captured in this analysis.

Take the target HR, for example. In phase 3 superiority trials, it is typically intended to reflect the minimal clinically important difference. However, no universally accepted threshold exists. While a given HR will always yield the same sample size mathematically under fixed assumptions—regardless of disease or context—the selection of a target HR is inherently subjective and context-dependent, shaped by disease characteristics, treatment mechanisms, outcome measures, and the perspectives of diverse stakeholders—including clinicians, sponsors, payors, professional societies, and patients. This variability is evident in our findings: for newly diagnosed GBM trials, the IQR of target HRs for OS was 0.6651–0.75. Although no significant differences were observed in target HRs among trials stratified by MGMT promoter methylation status or patient age, the small number of such trials (fewer than seven) limits the strength of these subgroup comparisons. Data on other diagnoses—particularly rare brain tumors—were also limited by low sample size. Therefore, the HR distributions reported here should not be interpreted as standard thresholds for future trials. Instead, target HRs should be determined collaboratively, with input from relevant stakeholders and tailored to the specific context of each trial.

Second, we relied on publicly available publications and protocols, which may incompletely report key design assumptions. Trials with missing or poorly described parameters may differ systematically from those with complete data, introducing potential bias. Third, our inclusion of only published and registered trials may result in selection bias, as unpublished or terminated studies—often reflecting feasibility or accrual challenges—were not captured. Fourth, we relied on published trial protocols and final reports, omitting updated or long-term follow-up data relevant to evolving survival trends. Fifth, our estimation of HRs in studies that did not report them relied on assumptions of constant hazards; while necessary for standardization, this approach may not fully reflect the true underlying survival dynamics in all trials. Last, we consolidated heterogeneous PFS definitions into a single category. While this enabled synthesis across trials—since biostatistical parameters like HRs are mathematically agnostic to disease context and endpoint definition when determining power and sample size—it may also obscure important differences in how progression was defined and assessed.

Conclusions and Broader Implications

Despite its limitations, this study provides the first systematic, quantitative benchmarks for the biostatistical parameters used to power neuro-oncology trials. While they provide a useful planning reference, they should not be applied in isolation from logistical and operational considerations. As such, they are not intended to be prescriptive but to serve as general reference points that support design transparency, justification, and modeling. For example, they may help guide expectations around clinical benefit (eg, target HR) and aid in protocol justification for stakeholders such as sponsors, patient groups, and regulatory agencies. They may also prove useful in future modeling efforts, including the development of Bayesian priors and trial simulations. Ultimately, we hope these benchmarks will promote more transparent and context-aware trial design, while also drawing attention to the persistent gap in consistent reporting of key design assumptions in clinical trial publications. More broadly, this benchmarking framework is adaptable to other areas of oncology to support the advancement of promising therapies.

Funding

National Institutes of Health/National Institute of General Medical Sciences (P20GM155899 to AMM’s institution); and the University of Louisville Presidential Scholar Award (to AMM). The funders of the study had no role in study design, data collection, data analysis, data interpretation, or writing of the report.

Conflict of interest statement

AMM consults for Neosoma, Inc., and received honorarium from GT Medical Technologies, Inc.

Author contributions

Conception/Design of the work/Data analysis/Data presentation: AMM. Acquisition of data: AMM, LAL, RAK, GG, BNS. Data interpretation: AMM, JB. Drafting the work: AMM, LAL, RAK, GG. Reviewing it critically for important intellectual content: AMM, RAK, IJA, AHM, GS, BJW, JB. Final approval of the version to be published: AMM, LAL, RAK, GG, BNS, IJA, AHM, GS, BJW, JB. Agreement to be accountable for all aspects of the work in ensuring that questions related to the accuracy or integrity of any part of the work are appropriately investigated and resolved: AMM, RAK, LAL, GG, BNS

Data Availability

All data collected and analyzed are available in the Supplemental Table. The R code used to analyze the data and reproduce the figures of this study is available at https://github.com/axitamm/NOTrialsBiostat.