Study of Vorasidenib (AG-881) in Participants With Residual or Recurrent Grade 2 Glioma With an IDH1 or IDH2 Mutation (INDIGO): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Vorasidenib (AG-881) in Participants With Residual or Recurrent Grade 2 Glioma With an IDH1 or IDH2 Mutation (INDIGO) (NCT04164901), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS).

2. Clinical Question

This question concerns the time until either of the specified events, not simply whether a participant experienced progression by a single fixed date. The record describes follow-up for the primary endpoint as up to approximately 30 months. The comparison therefore uses information about event timing and about participants who had not yet experienced an event when follow-up ended.

The clinical question is narrowly framed around participants with the specified tumor grade, mutation status, and treatment history. The record does not establish how the findings apply to people with other glioma grades, without an IDH1 or IDH2 mutation, or with different treatment histories. It also does not report a separate primary question about overall survival or quality of life.

3. Trial Design

This is a phase 3, multicenter, randomized, double-blind, placebo-controlled study with a parallel-group model. The registry record lists quadruple masking. Participants were assigned to vorasidenib or matching placebo; the brief summary describes a planned 1:1 allocation. The posted arm counts are 168 for vorasidenib and 163 for placebo. The record lists enrollment as 331 and describes approximately 340 participants as planned for randomization.

The intervention was vorasidenib 40 mg with continuous daily dosing. The comparator was matching placebo 40 mg with continuous daily dosing. Participants were required to have residual or recurrent grade 2 glioma with an IDH1 or IDH2 mutation and to have undergone surgery as their only treatment. Central confirmation of mutation status was required before randomization.

The primary endpoint was progression-free survival. The registry definition measures time from randomization to the first documented radiographic progression assessed by the blinded independent review committee under modified Response Assessment for Neuro-oncology for Low-Grade Gliomas, or death due to any cause, whichever occurred earlier. The stated timeframe was up to approximately 30 months. The record also lists secondary outcomes including time to next intervention, tumor growth rate, response outcomes, time to response, and duration of response.

The study status is active, not recruiting. The start date and primary completion date are recorded as 2020-01-05 and 2022-09-06. The registry record does not report the original sample-size justification, the detailed randomization procedure, or the operational details of masking. It does not report the protocol’s full statistical analysis plan.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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 Progression-Free Survival (PFS), measured over Up to approximately 30 months.

Progression-free survival (PFS) measures the time from randomization until the first of two events: radiographic disease progression documented by the blinded independent review committee, or death from any cause. The endpoint therefore incorporates both disease assessment and survival, with whichever event occurs first setting the recorded time. The committee assessment is described as using modified Response Assessment for Neuro-oncology for Low-Grade Gliomas criteria.

PFS is a time-to-event endpoint. It preserves information about when events occur and can include participants whose event has not been observed by the end of their available follow-up. Those participants are censored at the point their event status is no longer observed; censoring is a general feature of time-to-event analysis, but the registry record does not describe the detailed censoring rules used in this study.

This endpoint is used to compare the timing of progression or death between randomized groups, rather than to compare only the proportion with an event at one selected time. The registry reports the median PFS and a hazard ratio for the comparison. The median describes the point at which the estimated event-free proportion reaches one half, while the hazard ratio summarizes the relative event rates over follow-up under the model used. Neither measure alone describes every participant’s course, and the registry record does not report a separate result for overall survival.

7. Results Posted in the Registry

• Vorasidenib vs Matching Placebo: hazard ratio 0.39 (95% CI 0.27–0.56), reported p < 0.001 (as reported in the registry).

8. Secondary Efficacy Endpoints

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

Objective Response (OR) as Assessed by the Blinded Independent Review Committee (BIRC)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vorasidenib: 10.7% (18/168) versus 2.5% (4/163) on control; risk difference 8.3 percentage points (95% CI 3.0 to 13.5), risk ratio 4.37 (1.51–12.62); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Vorasidenib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Complete Response (CR) and Partial Response (PR) by BIRC

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vorasidenib: 1.2% (2/168) versus 0.0% (0/163) on control; risk difference 1.2 percentage points (95% CI -0.4 to 2.8); unadjusted two-proportion z-test p = 0.162.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vorasidenib and the control. The interval gives the range of effects that remain compatible with the data.

Progression-Free Survival (PFS) by the Investigator

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Kaplan-Meier); it was not recalculated.
• Result:
  • Vorasidenib vs Matching Placebo: hazard ratio 0.35 (95% CI 0.23–0.54), reported p < 0.001 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Vorasidenib vs Matching Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span response, progression, subsequent intervention, tumor growth, and response timing and duration. The posted findings include an objective-response result, a complete and partial response result, and an investigator-assessed PFS result. Results for the other listed secondary outcomes—including time to next intervention, tumor growth rate, time to response, and duration measures—are not reported in the registry record.

At a broad level, the available secondary findings are directionally consistent with the primary PFS comparison for objective response and investigator-assessed PFS. The complete and partial response comparison is less conclusive: the observed counts are sparse, and its unadjusted confidence interval includes no difference. These measures address different aspects of disease assessment. Response is a classification of observed change, whereas PFS concerns the timing of progression or death; agreement across them can be informative but does not make them interchangeable.

Secondary outcomes generally carry less confirmatory weight than a prespecified primary endpoint, particularly when many outcomes are examined. Testing multiple outcomes increases the chance of at least one apparently notable result arising by chance if no multiplicity adjustment is used. The registry record does not report whether a multiplicity adjustment, hierarchical testing strategy, or other control of multiple comparisons was planned. Thus, unadjusted secondary p-values should be interpreted cautiously and in the context of the full set of outcomes, rather than as independent proof.

The secondary results can add context to the primary finding, but they do not resolve the unreported questions about the other listed outcomes or about long-term effects beyond the stated assessment timeframe.

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

• Time to Next Intervention (TTNI)
• Tumor Growth Rate (TGR)
• Objective Response (OR) as Assessed by the Blinded Independent Review Committee (BIRC)
• Complete Response (CR) and Partial Response (PR) by BIRC
• Time to Response (TTR) by BIRC
• Time to CR+PR by BIRC
• Duration of Response (DoR)
• Duration of CR+PR

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis is a time-to-event comparison. This method is appropriate when the outcome is the time until progression or death and participants may have different lengths of follow-up. It can use the observed event times while accounting for participants whose event has not been observed by the end of their available observation. The registry identifies the Kaplan-Meier method for the reported PFS analysis and a Cox proportional-hazards analysis for the hazard ratio.

What does Kaplan-Meier estimation describe?

In general, a Kaplan-Meier estimate describes the probability of remaining event-free over time, while accounting for censoring under the method’s assumptions. The median is read from that estimated curve at the point where the estimated event-free proportion reaches one half. A median is not an average follow-up time, and it does not indicate that every participant experiences an event at that time. The registry record does not report the detailed censoring rules or the number at risk at each point in follow-up.

What does the hazard ratio describe?

The Cox proportional-hazards model estimates a hazard ratio comparing the event rate in one group with the event rate in the other, conditional on the model. A hazard is an instantaneous event rate among participants who have not yet experienced the event. A hazard ratio is not a risk ratio, a difference in median times, or a direct statement about the probability that a particular participant will experience progression or death.

The proportional-hazards assumption means, in general, that the relative hazards are treated as stable over time. If the relative hazards change over time, a single hazard ratio may not fully describe the pattern. The registry record does not report whether this assumption was assessed, how it was assessed, or whether another time-to-event model was used as a sensitivity analysis. The sponsor-reported hazard ratio is the relevant reported estimate for the primary comparison.

How should the p-value be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the statistical model. It does not give the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The primary p-value is reported as p < 0.001. The registry labels the reported analysis as a superiority analysis. The record does not report further detail about the testing hierarchy or the treatment of multiple endpoints.

How do the response comparisons differ?

Objective response and complete or partial response are binary outcomes: each participant is classified according to whether the response criterion was met. The posted unadjusted recalculation for objective response expresses the difference between the observed group proportions as a risk difference and gives a confidence interval and p-value. The sponsor-reported analysis uses the Cochran-Mantel-Haenszel method and reports an odds ratio. Odds ratios and risk differences are different measures, and analyses using different methods need not give identical estimates.

The posted recalculation is a simple unadjusted calculation from the summary counts. It does not replace a sponsor analysis that may use a different method. For complete and partial response, the small counts and the absence of events in one group make the estimate especially uncertain; the reported recalculated confidence interval includes zero. The registry record does not report a sponsor analysis for that comparison.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation is greater than a statistical model assumes. If ignored, uncertainty can be understated for some kinds of count data. The primary endpoint is time-to-event, and the record does not report an over-dispersion analysis for it. The registry also lists tumor growth rate as a secondary outcome but does not report its results in the posted secondary findings. No particular over-dispersion model or correction is reported in the registry record.

Overall, the endpoint-specific methods matter: survival analysis addresses event timing and censoring, whereas response analyses compare classifications. Interpretation should retain the distinction between sponsor-reported analyses and simple unadjusted recalculations based on posted summaries.

11. Confidence Intervals and Precision

A confidence interval describes the range of estimates compatible with the observed data under the method and assumptions used. It communicates uncertainty around an estimate; it is not a range containing a fixed proportion of individual participant outcomes. A narrower interval indicates greater statistical precision, while a wider interval indicates more uncertainty. The interval does not account for every possible source of bias or model misspecification.

For the primary PFS comparison, the reported hazard ratio is 0.39, with a 95% confidence interval from 0.27 to 0.56. The interval lies below one, which is consistent with a lower estimated event hazard for vorasidenib under the reported model. The interval also shows that the point estimate is not known without uncertainty. The reported p-value is p < 0.001, but that does not make the confidence interval irrelevant: the interval conveys the range of effect estimates compatible with the analysis.

The median estimates have their own uncertainty. The placebo median is 11.1 months, with a 95% confidence interval from 11.0 to 13.7 months. For vorasidenib, the median is 27.7 months and the lower confidence limit is 17.0 months; an upper confidence limit is not reported in the registry record. A missing upper limit should not be interpreted as a value of zero or as evidence that the median has no uncertainty.

For the investigator PFS analysis, the hazard ratio is 0.35, with a 95% confidence interval from 0.23 to 0.54. Its vorasidenib median has a lower confidence limit of 27.1 months, while its upper limit and median estimate are not reported in the registry record. The placebo median is 14.1 months, with a 95% confidence interval from 11.2 to 18.5 months. Differences between assessor-based analyses are possible and warrant attention when assessing robustness.

Confidence intervals also help contextualize response outcomes. The unadjusted risk-difference interval for objective response is 0.030 to 0.135. For complete and partial response, it is -0.004 to 0.028, which includes zero. These intervals concern the specific recalculated risk differences, not the sponsor’s odds-ratio analysis. In general, sparse outcomes can yield uncertain estimates even when the observed counts differ.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effects, not a reconstruction of the trial’s original design assumptions. The original sample-size justification and assumptions are not reported in the registry record. The stated illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; it considers detecting 100%, 75%, or 50% of the observed effect.

For time-to-event outcomes, the figures are the total number of events needed across the groups, not participants per arm. For the binary response outcome, the figures are participants per arm. The distinction matters: event counts are not interchangeable with participant counts because participants may have different follow-up and some may not experience the event during observation.

The 80% power column describes the illustrated number of events or participants needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect were present. The 90% power column applies the same idea at a higher target probability of detection. These are planning probabilities under assumptions, not guarantees about a future study.

Smaller effects generally require more information to detect reliably. Accordingly, the illustrations require more events or participants when planning for 75% or 50% of the observed effect than when planning for 100% of it. The event-based figures apply to the primary time-to-event analysis; the per-arm figures apply to the binary objective-response analysis. These figures are not observed power.

The accompanying curve is a way to view how the planning requirement changes across the effect assumptions. Its values should be interpreted according to the endpoint’s unit—total events for time-to-event analyses or participants per arm for the binary comparison—not as observed trial outcomes.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.390, so ln(HR) = -0.9416.
2. d = 4 × (1.96 + 0.842)² / [ln(0.390)]² = 35.4, rounded up to 36 events in total for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
hr <- 0.39                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(4164901)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 36 (80% power), 48 (90% power)
 75% of observed effect: events = 63 (80% power), 85 (90% power)
 50% of observed effect: events = 142 (80% power), 190 (90% power)
Simulated power with 36 events: 0.813 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 67 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 331 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 11.1          # control-arm median, months (converted from the posted unit)
hr          <- 0.39          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
   Analysis               Value Efficacy
  IA 1: 33%                   Z   3.7103
      N: 54         p (1-sided)   0.0001
 Events: 16        ~HR at bound   0.1530
  Month: 19    P(Cross) if HR=1   0.0001
            P(Cross) if HR=0.39   0.0338
  IA 2: 67%                   Z   2.5114
      N: 68         p (1-sided)   0.0060
 Events: 32        ~HR at bound   0.4071
  Month: 31    P(Cross) if HR=1   0.0060
            P(Cross) if HR=0.39   0.5603
      Final                   Z   1.9930
      N: 68         p (1-sided)   0.0231
 Events: 47        ~HR at bound   0.5586
  Month: 60    P(Cross) if HR=1   0.0250
            P(Cross) if HR=0.39   0.9000



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

15. Analyses Reported by the Sponsor

For the primary PFS endpoint, the registry reports a sponsor analysis using Kaplan-Meier and a Cox proportional-hazards model. The reported hazard ratio is 0.39, with a 95% confidence interval from 0.27 to 0.56 and p < 0.001. The primary comparison is the sponsor’s reported analysis, rather than a newly derived estimate from summary statistics.

The simple recalculations based on posted summaries are intended as checks or illustrations, not replacements for the sponsor’s analysis. The registry record does not flag a discrepancy for the primary result. For objective response, the sponsor reports a Cochran-Mantel-Haenszel odds ratio of 4.88, with a 95% confidence interval from 1.56 to 15.25 and p = 0.003. The unadjusted recalculation uses a risk difference instead, so the estimates are expressed on different scales and are not expected to match numerically.

The sponsor-reported method and the recalculated summary comparison answer related but not identical statistical questions. The sponsor analysis takes precedence when interpreting the sponsor’s stated result; the unadjusted recalculation helps describe what follows from the posted group summaries. The registry record does not report a sponsor analysis for complete and partial response.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are tested. Even if each test uses a conventional significance threshold, conducting many tests can increase the chance that at least one result appears statistically notable by chance. Common approaches include adjusting significance thresholds, specifying a hierarchy of tests, or labeling secondary analyses as exploratory. These are general options, not claims about what this study used.

The registry lists multiple secondary outcomes, including time to next intervention, tumor growth rate, objective response, complete and partial response, time to response, and duration measures. It reports findings for some secondary endpoints, but the registry record does not report a multiplicity strategy or testing hierarchy. The reported secondary p-values therefore should not automatically be interpreted as family-wise confirmatory evidence.

The registry record also does not report the detailed handling of missing endpoint data, loss to follow-up, censoring, or protocol deviations. These details matter because time-to-event estimates depend on how follow-up ends and how participants without an observed event are treated. The record does not report the full analysis-population definitions or whether all randomized participants were included in each endpoint analysis.

The record gives arm counts for the primary and posted secondary outcomes, but does not explain all differences among analysis denominators. The safety figures also use their own at-risk counts. Without the full protocol and analysis plan, it is not possible to determine from the registry record exactly how all exclusions, missing observations, or intercurrent events were handled. This limits independent assessment of the statistical procedures, not the ability to state the posted estimates.

These unreported details are important for judging how robust secondary findings are and how completely the posted results reflect randomized assignment. Their absence should be treated as a reporting limitation, not as evidence that a particular procedure was or was not used.

17. 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 (3.0%), suicidal ideation (1.2%), encephalopathy (0.6%), epilepsy (0.6%), partial seizures (0.6%).

The serious adverse event figures are counts of participants with at least one serious adverse event among those at risk for the reported safety measure. The registry lists 11 affected among 167 at risk in the vorasidenib group and 8 among 163 at risk in the matching placebo group. It reports no deaths in either group. These are descriptive safety counts; by themselves they do not establish that a treatment caused an event or explain differences between groups.

The listed serious-event terms include seizure at 3.0%, suicidal ideation at 1.2%, and encephalopathy, epilepsy, partial seizures, and toxic encephalopathy at 0.6% each. The record does not provide enough context in these entries to attribute each listed percentage to a specific group or to infer a comparative risk for each term. The group-level figures for participants with other adverse events are 158 among 167 at risk for vorasidenib and 152 among 163 at risk for placebo.

Serious adverse events and other adverse events are distinct reporting categories, and the counts should not be added together. The registry record does not report event duration, severity distributions beyond the serious-event classification, attribution, or detailed exposure-adjusted rates. The figures describe what was posted and should be interpreted with those limits.

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

The primary result describes a difference in PFS between randomized groups in this study population. The sponsor-reported hazard ratio is below one, its confidence interval is below one, and the reported p-value is small. The median PFS estimates also differ, with greater uncertainty around the vorasidenib median’s upper limit because that limit is not reported in the registry record. These findings are statistical comparisons of group outcomes over the reported follow-up, not predictions for an individual participant.

The result does not establish that every participant in one group had a longer PFS than every participant in the other group. Group distributions overlap, and an estimated hazard ratio summarizes relative event rates rather than a guaranteed change for each person. Nor does PFS directly answer whether overall survival differed; an overall-survival result is not reported in the registry record.

The study’s eligibility criteria define the population to which the comparison directly pertains: residual or recurrent grade 2 glioma with an IDH1 or IDH2 mutation after surgery as the only treatment. The record does not establish that the same estimates apply to other tumor grades, mutation statuses, or treatment histories. The primary timeframe is up to approximately 30 months, so the registry result does not answer questions about outcomes beyond that period.

The secondary findings provide additional context but have different endpoints and varying precision. The record does not report results for all listed secondary outcomes, and it does not report a multiplicity strategy. Consequently, those findings should not be treated as equivalent to the primary result or as a complete account of every outcome of interest.

Finally, statistical significance is not itself a judgment about clinical importance. Assessing clinical meaning requires context about the outcome, uncertainty, participant experience, and other benefits and harms. The registry statistics alone do not provide all of that context and should not be interpreted as medical advice.

19. Why This Trial Matters Statistically

This trial illustrates why the endpoint and its analysis must be read together. PFS is a time-to-event outcome, so the comparison uses event timing and accommodates incomplete observation rather than reducing follow-up to a single yes-or-no status. The Kaplan-Meier estimates and Cox-model hazard ratio summarize different features of that time course: the medians describe a point on the estimated event-free distribution, while the hazard ratio compares event rates under model assumptions.

It also demonstrates the importance of separating the primary result from secondary analyses. The primary endpoint has a sponsor-reported hazard ratio and confidence interval. Secondary outcomes include response classifications and investigator-assessed PFS, but they differ in measurement and precision. The registry record does not report how multiplicity was handled, so the secondary p-values need more cautious interpretation than a single prespecified primary test would.

The posted response counts show why effect measures and methods matter. A risk difference and an odds ratio express contrasts on different scales; a simple unadjusted recalculation need not match a sponsor analysis using another method. Likewise, sparse response counts can leave substantial uncertainty even when the observed group counts are different.

Finally, the record distinguishes reported estimates from what remains unknown. It provides confidence intervals for key comparisons but leaves some limits, analysis details, and secondary results unreported. That distinction is central to sound biostatistical interpretation: evidence can be informative without answering every clinical or methodological question.

20. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the full statistical analysis plan, the original sample-size justification, or detailed analysis-population definitions. It also does not describe the handling of missing data, censoring rules, or protocol deviations. These omissions limit independent evaluation of how the analyses were specified and implemented.

For the primary endpoint, the upper confidence limit for the vorasidenib median is not reported in the registry record. Results are described for follow-up up to approximately 30 months, so the record does not provide a basis for conclusions about longer-term PFS. The primary outcome is progression-free survival; a result for overall survival is not reported.

The registry record lists multiple secondary outcomes but reports findings for only some of them. It does not report a multiplicity approach, which limits the confirmatory interpretation of secondary tests. The response outcomes include sparse counts, and the complete and partial response result has a recalculated confidence interval that includes no difference. These features make precision and testing context important.

Safety entries are also limited. The record reports counts and selected serious-event terms but does not provide detailed attribution, event duration, or exposure-adjusted rates. The listed term percentages cannot be used to establish a comparative risk by group unless the relevant group attribution and denominator are clear.

Finally, the direct scope of inference is restricted to the described trial population and treatment history. The registry record does not provide evidence for other grades, mutation statuses, or prior treatment patterns. These limitations identify what the posted record can and cannot establish; they do not negate the reported primary comparison.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Vorasidenib (AG-881) in Participants With Residual or Recurrent Grade 2 Glioma With an IDH1 or IDH2 Mutation (INDIGO) — NCT04164901.
• Registry record last updated 2025-04-03; status last verified 2025-04.
• Results first posted 2023-11-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

The registry describes a phase 3, randomized, double-blind, placebo-controlled study of vorasidenib versus matching placebo in participants with residual or recurrent grade 2 glioma and an IDH1 or IDH2 mutation after surgery as their only treatment. The primary outcome is progression-free survival assessed by a blinded independent review committee, with follow-up up to approximately 30 months.

The reported primary comparison is a hazard ratio of 0.39, with a 95% confidence interval from 0.27 to 0.56 and p < 0.001. The registry also posts response and investigator-assessed PFS findings, along with limited safety counts. Important details—including the full statistical plan, multiplicity approach, missing-data handling, and results for several listed secondary outcomes—are not reported in the registry record.