Study Evaluating the Efficacy and Safety of Selinexor (KPT-330) in Participants With Recurrent Gliomas: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Evaluating the Efficacy and Safety of Selinexor (KPT-330) in Participants With Recurrent Gliomas (NCT01986348), a randomized phase 2 study. The primary outcome is 6-Month Progression-Free Survival (PFS) Rate.

2. Clinical Question

3. Trial Design

This was a Phase 2, open-label, multicenter study evaluating the efficacy and safety of oral selinexor in participants with recurrent gliomas. The registry record lists random allocation and no masking, but also identifies the study model as single-group. Results are posted for three nonsurgical treatment arms: Arm B received selinexor 50 mg/m^2 twice weekly, Arm C received 60 mg twice weekly, and Arm D received 80 mg once weekly. A separate surgery arm combined selinexor 60 mg with tumor resection. The complete dosing description for that arm is not reported in the registry record.

The registry lists enrollment of 76. The primary outcome results cover 24 participants in Arm B, 13 in Arm C, and 30 in Arm D. These are the arms included in the described modified intent-to-treat population; the primary result does not include a posted estimate for the surgery arm. The trial status is terminated. The reason for termination and the original target enrollment are not reported in the registry record.

The listed study dates are 2014-03-03 for study start and 2020-01-23 for primary completion. The registry also lists overall response rate, overall survival, progression-free survival, and treatment-emergent adverse events as secondary outcomes. It does not post reported analyses for the secondary outcomes in the analysis listing, although results are posted for overall response rate. The original statistical analysis plan, randomization procedures, allocation concealment, and the rationale for the chosen dose regimens are not reported in the registry record. The registry record therefore supports a description of the arms and posted outcomes, but not a detailed reconstruction of how the trial was designed or conducted.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 76 participants were enrolled, randomized and treated in this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat (mITT) population consisted of all enrolled participants in Arms B, C and D who had received at least 1 dose of study medication and have at least 1 post-baseline efficacy follow-up assessment, unless the participant discontinued treatment prior to the first post baseline assessment due to death, toxicity, or PD. Data for this outcome measure was not planned to be collected and analyzed for Arm A: Selinexor 60 mg and Surgery.

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: Safety population consisted of all participants who had received any amount of study treatment.

6. Primary Endpoint

The registry lists the primary outcome as 6-Month Progression-Free Survival (PFS) Rate, measured over From start of study treatment up to disease progression or death, whichever occurred first (assessed up to Month 6).

The primary endpoint is the 6-month progression-free survival rate, expressed as a percentage of participants. It is based on the estimated probability of being alive and without documented progression for at least 6 months after starting study treatment. Progression was defined by Response Assessment in Neuro-Oncology criteria. The listed criteria include at least a 25% increase in T1 gadolinium-enhancing disease, an increase in T2/FLAIR disease, detection of new lesions, or decreased clinical status. Death from any cause also counts as an endpoint event.

Progression-free survival is a time-to-event measure: it considers both whether an event occurred and when it occurred. The registry describes estimating the 6-month probability with the Kaplan-Meier method. This approach can use follow-up information from participants whose event status is not observed through the full follow-up period, while accounting for their observed time in the analysis. Interpretation depends on the quality of event assessment and censoring information, which is not reported in detail in the registry record.

A fixed-time PFS rate gives a clinically interpretable snapshot of disease control and survival at a stated follow-up point. It is not the same as overall response rate, which concerns tumor response, or overall survival, which considers death without including progression as an event. The primary endpoint estimates are imprecise, as reflected by their wide confidence intervals. They describe the posted results in these study arms; they do not establish a comparison with an untreated group or with another therapy.

7. Results Posted in the Registry

• Arm C: Selinexor 60 mg: 7.7% (1/13) versus 8.3% (2/24) on control; risk difference -0.6 percentage points (95% CI -18.9 to 17.6), risk ratio 0.92 (0.09–9.24); unadjusted two-proportion z-test p = 0.946.
• Arm D: Selinexor 80 mg: 16.7% (5/30) versus 8.3% (2/24) on control; risk difference 8.3 percentage points (95% CI -9.0 to 25.7), risk ratio 2.00 (0.42–9.42); unadjusted two-proportion z-test p = 0.365.

8. Secondary Efficacy Endpoints

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

Overall Response Rate (ORR)

• 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:
  • Arm C: Selinexor 60 mg: 7.7% (1/13) versus 8.3% (2/24) on control; risk difference -0.6 percentage points (95% CI -18.9 to 17.6), risk ratio 0.92 (0.09–9.24); unadjusted two-proportion z-test p = 0.946.
  • Arm D: Selinexor 80 mg: 10.0% (3/30) versus 8.3% (2/24) on control; risk difference 1.7 percentage points (95% CI -13.7 to 17.1), risk ratio 1.20 (0.22–6.61); unadjusted two-proportion z-test p = 0.834.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C: Selinexor 60 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm D: Selinexor 80 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists overall response rate, overall survival, progression-free survival, and treatment-emergent adverse events among the secondary outcomes. These outcomes address different aspects of treatment experience: tumor response, survival duration, disease progression, and safety. Overall response rate is the additional secondary outcome with arm-specific estimates posted in the results. The analysis listing does not include reported analyses, and detailed numerical results for all listed secondary outcomes are not present there.

The overall response results add a separate view of tumor response, but they do not resolve uncertainty in the primary 6-month PFS estimates. Response and PFS are related measures of disease status, yet they are not interchangeable. A response outcome does not incorporate the same time-to-event information as PFS, while PFS includes both progression and death. Likewise, overall survival focuses on death and cannot be inferred from PFS or response rates alone.

The secondary comparisons are unadjusted recalculations. When several endpoints and arm comparisons are examined, the chance of at least one apparently notable result can increase unless multiplicity is addressed. The registry record does not report a prespecified multiplicity strategy, so the secondary results should be treated as exploratory rather than as confirmatory evidence. A result from a secondary outcome also carries less weight when its analysis plan, hierarchy, and relationship to the primary endpoint are not documented.

The overall pattern must therefore be read alongside the small arm sizes, broad uncertainty, and incomplete statistical documentation. Secondary outcomes may help describe the trial, but they do not provide a substitute for a precise primary result or an external comparator. No conclusion about overall survival can be drawn from the listed outcome names alone.

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

• Overall Response Rate (ORR)
• Overall Survival (OS)
• Progression-free Survival (PFS)
• Number of Participants With Treatment-emergent Adverse Events (TEAEs) and Treatment-emergent Serious Adverse Events (TESAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event endpoint reported as a rate at a fixed follow-up time. The registry says that the estimated survival probability of remaining progression-free for at least 6 months was calculated using the Kaplan-Meier method. In general, Kaplan-Meier estimation uses each participant’s observed time to an event or last known follow-up. A participant without a recorded event by their last observation can be censored: their available follow-up contributes information up to that point, without treating them as if they remained event-free indefinitely. The registry record does not provide the censoring rules or a detailed account of follow-up completeness.

For this endpoint, an event is the first documented progression under the stated RANO criteria or death from any cause. Combining these events means the endpoint captures time until either disease progression or death, rather than time to tumor response or death alone. The 6-month rate is an estimate at a selected time point, not a simple percentage calculated solely from participants with complete follow-up at that time. The registry describes a modified intent-to-treat population for Arms B, C, and D, but the population definition is cut off. Its complete implementation and any exclusions are not reported in the registry record.

Each arm’s estimate is accompanied by a 95% confidence interval. In general, a confidence interval expresses the uncertainty associated with an estimate under the statistical method used. A wider interval indicates less precision; a narrow interval indicates greater precision. Confidence intervals are not guarantees about an individual participant’s outcome. In these results, the intervals are broad, which is consistent with the limited number of participants in each arm and the sparse outcome information. The registry record does not identify the interval construction method for the primary results.

The comparison estimates and p-values posted alongside the arm results are labelled as unadjusted recalculations. In general, an unadjusted comparison assesses the observed contrast without accounting for additional covariates or other adjustments. A p-value describes how compatible the data are with a specified null hypothesis under the test assumptions; it is not the probability that the null hypothesis is true. The unadjusted p-values do not establish equivalence or rule out important differences. The registry record reports no analyses in its analysis listing, so the posted recalculations should not be mistaken for a documented sponsor analysis plan. No discrepancy is flagged between the posted results and recalculations.

The registry lists allocation as randomized, masking as none, and the model as single-group. These labels do not explain how randomization was implemented, whether allocation was stratified, or how the single-group model relates to the separate treatment arms. Those details are not reported in the registry record. Because the arms used different schedules and include a distinct surgery group, arm-level outcomes should not be treated as a clean dose comparison without information about eligibility, assignment, and baseline characteristics.

Why can sparse data make estimates uncertain?

When few participants contribute information to an outcome, each event or change in follow-up can have a relatively large influence on the estimated rate. This can lead to wide confidence intervals and unstable comparisons. The primary outcome arms include 24, 13, and 30 participants, respectively. The estimate for Arm C has the widest interval among the posted primary results. The registry does not provide a formal sample-size justification or detail the number of participants expected to contribute to the endpoint at each follow-up time.

Why does over-dispersion matter?

In general, over-dispersion occurs when observed variability exceeds what a statistical model assumes. For count or rate outcomes, ignoring over-dispersion can make uncertainty appear smaller than it is. The primary endpoint is a Kaplan-Meier time-to-event estimate, and the registry does not report an over-dispersion model or describe its use. It would therefore be inappropriate to assume that an over-dispersion adjustment was performed or needed for the posted Kaplan-Meier estimates.

What is not documented about the statistical plan?

The registry record does not report the original sample-size justification, planned interim analyses, a complete statistical analysis plan, or prespecified procedures for multiplicity. It also does not give full details on missing data, censoring, stratification, or adjustment for prognostic factors. These omissions limit assessment of whether the posted analyses match the original plan and how confidently they support comparisons among arms. The study’s Phase 2 designation and the results listing do not fill in those missing methodological details.

11. Confidence Intervals and Precision

The primary 6-month PFS estimates have wide 95% confidence intervals: 2.67% to 35.39% for Arm B, 1.17% to 50.57% for Arm C, and 7.77% to 38.27% for Arm D. The width of these ranges means the estimated rate is not very precise. The point estimate is only one location within a broader set of values compatible with the data and the method. These intervals do not mean that every value within them is equally likely, and they do not predict an individual participant’s outcome.

Small arm sizes contribute to limited precision, particularly when the endpoint is a time-to-event outcome and the amount of observed follow-up or number of events is limited. The registry does not report the number of events underlying each Kaplan-Meier estimate, detailed censoring information, or an interval construction method. That makes it difficult to assess how much each arm’s estimate depends on follow-up patterns or specific observations.

The posted comparisons are also uncertain. Their unadjusted p-values are 0.946 for Arm C versus Arm B and 0.365 for Arm D versus Arm B. The reported uncertainty intervals for the recalculated contrasts include values on both sides of no difference. This means the data do not precisely distinguish between an advantage for either arm and little or no difference. The results should not be interpreted as proof of equality.

Confidence intervals help show why a point estimate alone can overstate certainty. Differences in point estimates across arms may appear noticeable, yet broad intervals and small groups mean that the underlying arm-specific rates remain uncertain. The registry record does not report a prespecified precision target or the sample-size assumptions used for the trial’s original design.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations express required sample sizes as participants per arm, not total events. They are based on the observed effect and use the assumptions stated with the illustrations: a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that a hypothetical study would need, under those assumptions, to have an 80% chance of detecting the specified effect if that effect were real. The 90% power column describes the corresponding planning target for a 90% chance. These are planning calculations, not a statement about how likely the completed trial was to find a result, and not observed power. They do not show that the trial was adequately powered for its original aims.

The rows that plan for 100%, 75%, or 50% of the observed effect are alternative assumptions about the size of a future effect worth detecting. Smaller effects are harder to distinguish from random variation and therefore require more participants. The illustrations can become very large when the observed contrast is small, reflecting the difficulty of detecting a modest difference with conventional significance and power assumptions.

These calculations use the observed estimates as their starting point, so they should be treated cautiously, particularly when arm sizes are limited and estimates are imprecise. They are not a reconstruction of the actual protocol’s sample-size justification. The registry record does not report the trial’s original target effect, planned allocation details, dropout assumptions, or any adjustment to the original sample-size target.

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 = 0.083; treatment proportion p₁ = 0.077; average p̄ = 0.080.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3839 = 0.7525.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3839 = 0.3231.
4. n = (0.7525 + 0.3231)² / (-0.0064)² = 28,156.7, rounded up to 28,157 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 <- 0.0833333333333333                          # control proportion
p1 <- 0.0769230769230769                          # 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(1986348)
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 = 28,157 (80% power), 37,694 (90% power)
 75% of observed effect: n per arm = 50,514 (80% power), 67,624 (90% power)
 50% of observed effect: n per arm = 114,683 (80% power), 153,528 (90% power)
power.prop.test: 28156.7 
Simulated power at n = 28,157 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and several secondary outcomes, but it does not report a prespecified multiplicity strategy. Multiplicity arises when researchers examine several outcomes, treatment arms, time points, or statistical comparisons. Each additional test creates another opportunity for a result to appear notable by chance. Common approaches can control the overall error rate or organize outcomes into a prespecified hierarchy, but the registry record does not say whether any such approach was planned or used.

The comparisons between Arms C and D and Arm B are presented with unadjusted p-values. The secondary outcome comparisons are likewise described as unadjusted recalculations. These values do not account for the collection of outcomes and comparisons across the study. They are useful as descriptive statistical summaries, but should not be treated as multiplicity-adjusted confirmatory tests. No discrepancy is flagged, but the registry does not list sponsor analyses for these comparisons.

The full analysis populations are also not completely documented. The primary outcome description gives a modified intent-to-treat definition for Arms B, C, and D, including treatment exposure and post-baseline assessment criteria, but the description ends mid-sentence. The complete criteria, participant flow, and any exclusions are not reported in the registry record. The record lists 76 enrolled participants, while the primary outcome results cover the three nonsurgical arms. The relationship between overall enrollment and the outcome analysis population is not fully explained.

Missing-data methods, censoring rules, and sensitivity analyses are not reported in the registry record. These details matter for a Kaplan-Meier endpoint because incomplete follow-up can affect how much information contributes at later time points. The registry also does not report planned interim analyses, the original sample-size justification, or a complete statistical analysis plan. Without these details, readers cannot determine how the analyses were prespecified or whether all relevant analysis decisions are documented.

15. 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 (21.4%), diarrhoea (12.5%), meningitis bacterial (12.5%), staphylococcal infection (12.5%), decreased appetite (12.5%).

The safety results count participants with treatment-emergent serious adverse events and other treatment-emergent adverse events in each arm. For serious adverse events, the registry lists 5 of 8 participants in the surgery arm, 7 of 24 in Arm B, 7 of 14 in Arm C, and 7 of 30 in Arm D as affected. For other treatment-emergent adverse events, all participants at risk in each listed arm are recorded as affected: 8 of 8, 24 of 24, 14 of 14, and 30 of 30, respectively. These counts describe the posted safety groups; they do not establish that selinexor caused each event.

The registry’s listed serious event terms include seizure at 21.4%, and diarrhoea, bacterial meningitis, staphylococcal infection, decreased appetite, and cerebrospinal fluid leakage at 12.5% each. The record does not clarify in this summary the denominator or whether these term frequencies are pooled across arms. It also lists deaths in each arm, but the recorded counts do not by themselves establish cause or treatment relationship. The safety figures should be read as descriptive, with the registry record’s limited detail in mind.

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

The posted results provide arm-specific estimates of 6-month PFS among participants in three nonsurgical selinexor regimens. The estimates are accompanied by broad confidence intervals, and the unadjusted comparisons do not precisely distinguish the arms. The results therefore describe what was observed in these groups, while leaving substantial uncertainty about the underlying rates and any differences between regimens.

The record does not include a posted untreated or active comparator. Although it records random allocation, the model is also labelled single-group and the allocation process is not described. Without a clear account of how participants entered the arms and how baseline characteristics compared, the arm results cannot establish that any observed difference was caused by dose or schedule. Nor do nonsignificant unadjusted p-values demonstrate that regimens are equivalent.

The study is registered as terminated, but the reason is not reported in the registry record. That status should not be interpreted as evidence about efficacy or safety. The registry does not report enough information to attribute termination to a particular outcome, operational issue, or other cause.

The endpoint is clinically interpretable as remaining alive without documented progression through 6 months, but it is not a complete account of benefit or harm. Overall survival, response, and adverse events address distinct questions. The available registry results do not provide a complete analysis of all listed outcomes, the original statistical plan, or detailed missing-data procedures. Accordingly, the results do not support a definitive comparative conclusion, a claim of treatment effect, or a recommendation for clinical care. They are best understood as descriptive Phase 2 registry findings whose precision and interpretation are constrained by the small arm sizes and incomplete reporting.

17. Why This Trial Matters Statistically

This trial illustrates the difference between a point estimate and the strength of evidence behind it. The 6-month PFS rates provide a straightforward summary for each posted arm, but their wide confidence intervals show that the estimates remain uncertain. Looking at the interval and the amount of information behind an estimate is essential; ranking arms by their point estimates alone would overstate what these data establish.

The record also highlights how design labels and analysis populations affect interpretation. Random allocation is recorded, yet the model is labelled single-group, and the assignment process is not described. The primary outcome is reported for the three nonsurgical arms, while the study also includes a surgery arm. Without fuller population and allocation details, arm comparisons remain difficult to interpret as causal contrasts.

Finally, this example shows why registered outcomes, analysis reporting, and statistical planning matter. The record lists several secondary outcomes, but the analysis listing contains no reported analyses; it also does not report multiplicity procedures, the original sample-size justification, or a full statistical analysis plan. Those omissions do not invalidate the posted estimates, but they limit how confidently readers can distinguish planned confirmatory findings from exploratory descriptions. The result is a useful case in interpreting registry evidence cautiously and separating what is estimated from what remains unknown.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations constrain interpretation. The registry record gives both randomized allocation and a single-group model without explaining how these descriptions fit together. It does not report the randomization method, allocation concealment, baseline balance, or whether treatment assignment was stratified. This is particularly relevant when considering comparisons among dose schedules and the surgery arm.

The registry lists enrollment of 76, but the primary outcome results cover the three nonsurgical arms and not the surgery arm. The mITT population definition is truncated, and complete participant flow is not reported. The record does not explain why the results population is smaller than the enrollment figure or how participants without post-baseline efficacy assessments were handled.

The primary confidence intervals are wide, and the arm sizes are limited. Event counts underlying the Kaplan-Meier estimates, detailed follow-up distributions, censoring rules, and sensitivity analyses are not reported in the registry record. The reason for termination is also not reported. These gaps prevent a thorough assessment of outcome ascertainment, missing information, and the robustness of the estimates.

The record does not provide a complete statistical analysis plan, original sample-size justification, multiplicity strategy, or details of any interim analyses. Secondary results are therefore difficult to place in a prespecified testing framework. The safety summary lists affected participants and selected serious event terms, but does not provide enough detail to assess event timing, severity patterns, exposure duration, or causal attribution. These limitations are specific to the available registry record and should inform how much weight is placed on its descriptive findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study Evaluating the Efficacy and Safety of Selinexor (KPT-330) in Participants With Recurrent Gliomas — NCT01986348.
• Registry record last updated 2023-01-26; status last verified 2023-01.
• Results first posted 2021-08-02.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01986348 is a Phase 2, open-label, multicenter study evaluating oral selinexor in recurrent gliomas. It lists random allocation, no masking, and a single-group model, but does not explain the relationship among those design labels. The study status is terminated; the reason is not reported in the registry record.

The primary endpoint is 6-month PFS, estimated by Kaplan-Meier methods. Results are posted for Arms B, C, and D, with arm sizes of 24, 13, and 30. Their estimates have broad 95% confidence intervals, and unadjusted comparisons do not precisely distinguish the groups. The registry lists overall response, overall survival, PFS, and treatment-emergent adverse events as secondary outcomes, but complete analysis reporting and statistical planning details are not reported.

The findings are descriptive and uncertain. The registry record does not provide a complete account of the analysis population, randomization procedures, missing-data handling, multiplicity, or original sample-size rationale. They do not establish comparative treatment effects.