Comparison of Veliparib and Whole Brain Radiation Therapy (WBRT) Versus Placebo and WBRT in Adults With Brain Metastases From Non-Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Veliparib and Whole Brain Radiation Therapy (WBRT) Versus Placebo and WBRT in Adults With Brain Metastases From Non-Small Cell Lung Cancer (NCT01657799), a randomized phase 2 study. The primary outcome is Overall Survival.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel-group phase 2 study. Its official title describes it as dose-ranging. The registry record lists AbbVie (prior sponsor, Abbott) as sponsor and gives the status as completed. The recorded start date is 2012-10-19, and the primary completion date is 2015-01-22. The reported enrollment was 307.

Participants were assigned to one of three regimens: placebo twice daily plus WBRT, veliparib 50 mg twice daily plus WBRT, or veliparib 200 mg twice daily plus WBRT. The active drug or placebo was taken orally concomitantly with radiation. Each group received 30.0 Gy of WBRT, delivered in 10 daily fractions of 3.0 Gy, excluding weekends and holidays. Thus, the randomized contrast evaluates the veliparib regimens against placebo when both are combined with WBRT; it does not estimate the effect of WBRT itself.

The primary outcome analysis lists 102 participants for placebo, 103 for veliparib 50 mg, and 102 for veliparib 200 mg. These are the numbers attached to the posted outcome estimates, while the overall enrollment is 307. The primary outcome was assessed from randomization up to 36 months. The listed secondary outcomes—best tumor response rate, time to intracranial progression (radiographic), and time to clinical brain metastasis progression—were assessed from randomization up to 24 months.

The registry record does not report the original sample-size justification, planned allocation ratio, or additional details of the randomization procedure. It identifies the study as double-blind but does not specify which roles were masked. Specific protocol details beyond the listed regimens and endpoints are not reported in the registry record.

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: Subjects were randomized in a 1:1:1 ratio to one of three treatment groups. Randomization was stratified by graded prognostic assessment (GPA) score (≤ 2.5 versus \> 2.5) and neurological symptoms (symptomatic versus asymptomatic).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival, measured over From randomization up to 36 months.

Overall survival was defined as the number of days from randomization to death. Deaths counted whether they occurred while a participant was still taking study treatment or after treatment had been discontinued. For participants not known to have died, follow-up was censored at the date they were last known to be alive. The stated timeframe was from randomization up to 36 months, and the analysis population was all randomized participants.

Overall survival is a time-to-event endpoint: it uses both whether a death was observed and the time until that event, while accounting for participants whose observed follow-up ends before a recorded death. A median gives the time by which half of the estimated group survival distribution has experienced the event. It does not mean that every participant lived for that duration, nor does it describe an individual’s expected survival.

In general, time-to-event outcomes are useful when follow-up duration varies or some participants have no recorded event by the end of observation. Censoring allows their available follow-up to contribute without treating the last known alive date as a death. The validity of this approach depends on assumptions about censoring and follow-up; the registry record does not report diagnostics or further assumptions. Overall survival is a direct endpoint based on death, but the posted group summaries alone do not describe every feature of the survival curves or the experience of individual participants.

7. Results Posted in the Registry

• Placebo BID + WBRT vs Veliparib 50 mg BID + WBRT: hazard ratio 0.98 (95% CI 0.72–1.35), reported p = 0.927 (as reported in the registry).
• Placebo BID + WBRT vs Veliparib 200 mg BID + WBRT: hazard ratio 0.98 (95% CI 0.71–1.35), reported p = 0.906 (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.

Best Tumor Response Rate

• 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:
  • Veliparib 50 mg BID + WBRT: 36.9% (38/103) versus 41.2% (42/102) on control; risk difference -4.3 percentage points (95% CI -17.6 to 9.1), risk ratio 0.90 (0.64–1.26); unadjusted two-proportion z-test p = 0.530.
  • Veliparib 200 mg BID + WBRT: 42.2% (43/102) versus 41.2% (42/102) on control; risk difference 1.0 percentage points (95% CI -12.5 to 14.5), risk ratio 1.02 (0.74–1.42); unadjusted two-proportion z-test p = 0.887.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Veliparib 50 mg BID + WBRT 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 Veliparib 200 mg BID + WBRT and the control. The interval gives the range of effects that remain compatible with the data.

Time to Intracranial Progression (Radiographic)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Cox proportional hazard model); it was not recalculated.
• Result:
  • Placebo BID + WBRT vs Veliparib 50 mg BID + WBRT: hazard ratio 1.30 (95% CI 0.78–2.17), reported p = 0.313 (as reported in the registry).
  • Placebo BID + WBRT vs Veliparib 200 mg BID + WBRT: hazard ratio 1.18 (95% CI 0.70–2.00), reported p = 0.534 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo BID + WBRT vs Veliparib 50 mg BID + WBRT and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo BID + WBRT vs Veliparib 200 mg BID + WBRT and the control. The interval gives the range of effects that remain compatible with the data.

Time to Clinical Brain Metastasis Progression

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Cox proportional hazard model); it was not recalculated.
• Result:
  • Placebo BID + WBRT vs Veliparib 50 mg BID + WBRT: hazard ratio 1.05 (95% CI 0.63–1.75), reported p = 0.860 (as reported in the registry).
  • Placebo BID + WBRT vs Veliparib 200 mg BID + WBRT: hazard ratio 1.29 (95% CI 0.80–2.09), reported p = 0.289 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo BID + WBRT vs Veliparib 50 mg BID + WBRT and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo BID + WBRT vs Veliparib 200 mg BID + WBRT and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address different aspects of disease course: best tumor response rate, time to intracranial progression assessed radiographically, and time to clinical brain metastasis progression. These outcomes complement overall survival by describing response and progression rather than death. Taken together, the posted comparisons do not form a consistent pattern that clearly favors adding either veliparib dose across all these measures.

That broad pattern is compatible with the primary overall-survival result, which also does not show a clear separation between either veliparib group and placebo in this trial. However, secondary endpoints are not interchangeable with overall survival, and a result on response or progression cannot by itself establish a corresponding effect on survival. Differences in endpoint definitions, follow-up windows, and analysis methods also mean that each outcome answers a distinct question.

Secondary findings generally carry less inferential weight when many outcomes or comparisons are tested, because the chance of observing at least one apparently unusual result increases as the number of tests grows. The registry record lists multiple outcomes and analyses but does not report a multiplicity adjustment or a testing hierarchy. Therefore, the secondary p-values should not be treated as if each were an isolated, pre-specified test with no other comparisons. This caution applies even when an individual result appears more notable than the rest.

The secondary analyses can still be informative as descriptive and supportive evidence, especially when interpreted alongside the primary endpoint and the study design. Their role is to add context, not to overturn the main result based on a single unadjusted comparison. The registry record does not report additional analyses that would clarify whether the secondary results were confirmatory, exploratory, or prioritized in a formal sequence.

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

• Best Tumor Response Rate
• Time to Intracranial Progression (Radiographic)
• Time to Clinical Brain Metastasis Progression

9. Statistical Interpretation

10. Statistical Methods Explained

How should a median survival time be read?

For a time-to-event outcome, the median is the point at which the estimated survival experience reaches the halfway mark. The reported median overall survival was 185.0 days with placebo, and 209.0 days in each veliparib group. This is a group-level summary. It is not a statement that each participant survived for that length of time, and it does not capture the full shape of the survival experience. The confidence interval communicates uncertainty in the median estimate.

What does a hazard ratio describe?

A hazard ratio compares event rates over follow-up between groups under a time-to-event model. A value of 1 represents equal hazards under the model; values on either side represent different relative hazards, with direction depending on which group is the numerator and how the comparison is coded. The registry lists placebo-versus-veliparib comparisons and reports hazard ratios of 0.985 and 0.981 for overall survival. Both are close to 1. Their 95% confidence intervals include 1, so the estimates are not precise enough to distinguish the comparisons from equal hazards at the conventional two-sided 0.05 level. A hazard ratio is not a ratio of median survival times and does not by itself describe an absolute difference in days.

The sponsor used a Cox proportional hazard model for the reported hazard ratios. In general, a Cox model estimates a relative hazard while allowing the underlying baseline hazard to remain unspecified. Its usual interpretation relies on a proportional-hazards assumption: the relative hazard is treated as stable over time. Whether that assumption was examined, and any diagnostics or model adjustments, are not reported in the registry record. The sponsor also reported log-rank tests for overall survival. In general, the log-rank test compares event-time patterns across groups while incorporating censored observations; the registry lists p-values of 0.933 and 0.909 for the two comparisons.

What does censoring contribute?

Some participants may be alive at their last recorded follow-up, so their exact eventual survival time is unknown. The primary endpoint description says such participants were censored at their last known alive date. In general, censoring means that their follow-up contributes information up to that point without counting them as having died. The analysis depends on assumptions about how censoring relates to the event process. Additional details about follow-up completeness or censoring diagnostics are not reported in the registry record.

How are the secondary outcome methods different?

Best tumor response rate is a binary outcome expressed as a percentage of participants. Its posted comparisons include risk differences, and the registry reports Cochran-Mantel-Haenszel tests. In general, a risk difference expresses the difference between two group proportions, while a Cochran-Mantel-Haenszel test can assess an association across strata. The registry record does not describe the strata or any adjustment details. The reported tests for the response comparisons have p-values of 0.535 and 0.898.

Time to intracranial progression and time to clinical brain metastasis progression are also time-to-event outcomes. Their reported group summaries are medians with confidence intervals, and their comparisons include hazard ratios from Cox models and log-rank tests. These endpoints are distinct from overall survival: they concern progression rather than death. Their observation timeframe was from randomization up to 24 months.

What should be understood about the planning illustrations?

The planning illustrations use the observed effect as a starting point, then consider detecting the full observed effect or a stated fraction of it. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The time-to-event illustrations express the requirement as total events, using the Schoenfeld approach; the other illustrations express it as participants per arm. These are hypothetical planning calculations, not the trial’s original sample-size justification. The trial’s original design assumptions are not reported in the registry record. Smaller effects require more information to detect under the stated assumptions.

General statistical interpretation also depends on the analysis plan, outcome definitions, handling of missing information, and any adjustments for multiple comparisons. The registry record gives some endpoint definitions and reported methods, but does not provide a complete statistical analysis plan. Details such as model diagnostics, covariate adjustment, handling of missing secondary outcomes, and multiplicity procedures are not reported. Those gaps limit how fully the posted estimates can be assessed beyond the methods explicitly named.

11. Confidence Intervals and Precision

Confidence intervals indicate how much uncertainty surrounds an estimated quantity under the analysis method. They are not ranges containing every participant’s outcome, and they do not guarantee that the true value lies within the interval. A 95% confidence interval is a repeated-sampling procedure: under its assumptions, intervals constructed in the same way would include the underlying parameter in 95% of repetitions.

For overall survival, the median confidence intervals are 137.0 to 251.0 days for placebo, 169.0 to 264.0 days for veliparib 50 mg, and 138.0 to 255.0 days for veliparib 200 mg. The intervals overlap, and the group medians are not estimated without uncertainty. The Cox-model estimates also have broad intervals: 0.716 to 1.355 for the 50 mg comparison and 0.710 to 1.354 for the 200 mg comparison. Both include 1, the value corresponding to equal hazards. This means the estimated relative hazards are not sharply separated from that reference value.

Precision is different from whether a test crosses a significance threshold. A non-significant p-value does not show that two groups are equivalent; it indicates that the data do not provide strong evidence against the tested null under that method. The width of the confidence interval is important because it shows the range of effect sizes that remain compatible with the data and model. The posted intervals do not identify a single precise treatment contrast.

For medians, the registry reports an upper confidence limit of “null” for some secondary estimates. An absent limit is not a numerical estimate and should not be interpreted as a precisely known boundary. The record does not explain why those limits are unavailable. Overall, the posted results support cautious reading of the magnitude and direction of effects rather than a definitive claim of equality or difference.

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 hypothetical sample-size illustrations based on the observed effect, not the trial’s original design justification. For binary outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events across the comparison, not participants per arm. These units matter: an event target is not interchangeable with an enrollment target, because participants may have different follow-up and event status.

The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For time-to-event outcomes, the calculation uses the Schoenfeld approach. Each planning scenario uses the full observed effect or a stated fraction of that effect. The columns for 80% and 90% power describe the number of events or participants that the assumptions indicate would be needed to have an 80% or 90% chance, respectively, of detecting the specified effect if that effect were the true one and the assumptions held. They are planning targets, not a description of what happened in the trial.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants or events when the effect to detect is reduced. The figures are therefore sensitive to the observed effect used as their starting point; they should not be treated as reliable forecasts of a future study without considering its population, design, follow-up, and analysis plan. These figures are not observed power.

The original sample-size rationale, target power, and planned assumptions for this trial are not reported in the registry record. The illustrations instead show what a new planning calculation would imply under the stated assumptions. They do not establish whether the completed trial was adequately sized for its original objectives.

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 = 0.985, so ln(HR) = -0.0151.
2. d = 4 × (1.96 + 0.842)² / [ln(0.985)]² = 137,445.2, rounded up to 137,446 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 <- 0.985                              # 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(1657799)
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 = 137,446 (80% power), 184,001 (90% power)
 75% of observed effect: events = 244,348 (80% power), 327,112 (90% power)
 50% of observed effect: events = 549,781 (80% power), 736,001 (90% power)
Simulated power with 137,446 events: 0.800 (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 203,409 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 307 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 <- 6.08219178082192          # control-arm median, months (converted from the posted unit)
hr          <- 0.985          # 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: 125224         p (1-sided)   0.0001
  Events: 62058        ~HR at bound   0.9707
      Month: 15    P(Cross) if HR=1   0.0001
                P(Cross) if HR=0.98   0.0338
      IA 2: 67%                   Z   2.5114
      N: 200176         p (1-sided)   0.0060
 Events: 124115        ~HR at bound   0.9858
      Month: 24    P(Cross) if HR=1   0.0060
                P(Cross) if HR=0.98   0.5603
          Final                   Z   1.9930
      N: 203410         p (1-sided)   0.0231
 Events: 186172        ~HR at bound   0.9908
      Month: 60    P(Cross) if HR=1   0.0250
                P(Cross) if HR=0.98   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

The posted primary comparisons are the sponsor-reported analyses. The registry gives Cox-model hazard ratios for overall survival of 0.985 for placebo versus veliparib 50 mg and 0.981 for placebo versus veliparib 200 mg, with 95% confidence intervals and reported p-values. It also gives log-rank test results for each comparison. Those are the principal reported inferential results for the primary endpoint.

The secondary response comparisons include sponsor-reported Cochran-Mantel-Haenszel p-values, while the progression outcomes include reported log-rank p-values. The statistical methods named in the record are therefore not identical across endpoints: binary response is assessed with a different test than the time-to-event outcomes. Details of the sponsor’s full analysis plan, including model covariates, strata, and diagnostic checks, are not reported in the registry record.

Some displayed calculations are simple, unadjusted re-calculations from posted summary statistics and are distinct from the sponsor’s inferential analysis. They can help readers see an unadjusted contrast, but they do not replace the sponsor’s analysis or reconstruct all of its assumptions. The registry record does not flag a discrepancy between the sponsor’s analysis and the recalculated results. Where the sponsor’s reported method and result are available, they are the primary account of the trial’s analysis; a simple recalculation should be read as supplementary rather than as a correction.

The planning illustrations are separate again: they use observed effects to explore hypothetical requirements under specified assumptions. They are not the sponsor’s original design rationale and do not indicate achieved power.

16. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and three secondary outcomes, as well as multiple comparisons across treatment groups. It reports tests for the primary and secondary outcomes, but does not report a multiplicity adjustment, a hierarchy for testing endpoints, or a plan identifying which comparisons were confirmatory. When several hypotheses are tested, the chance of at least one apparently positive result can increase. General methods for addressing this include adjusting significance thresholds or specifying an ordered testing strategy; whether either approach was used in this trial is not reported in the registry record.

Missing-data information is also limited. For overall survival, the endpoint definition says that participants not known to have died were censored at the date they were last known to be alive. This describes the handling of incomplete event follow-up for the primary time-to-event endpoint, but does not provide the amount or pattern of censoring by group. The registry record does not report imputation methods or detailed missing-data procedures for the secondary outcomes.

The primary outcome population is identified as all randomized participants. That helps clarify which participants the primary result is intended to represent, but it does not by itself describe the exact analysis implementation, adherence to assigned treatment, or treatment discontinuations. The registry record does not report a detailed analysis population definition for every secondary endpoint or provide a full statistical analysis plan.

These omissions do not erase the posted estimates, but they limit assessment of how the analyses handled multiple testing, incomplete observations, and deviations from assigned treatment. They also make it difficult to distinguish confirmatory findings from exploratory results. Interpretations should therefore emphasize the reported estimates and their uncertainty while avoiding stronger claims than the registry record supports.

17. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: malignant neoplasm progression (15.7%), pneumonia (7.9%), brain oedema (4.0%), pain (3.0%), seizure (3.0%).

The posted safety counts show serious adverse events in 39 of 101 participants at risk in the placebo plus WBRT group, 31 of 103 at risk in the veliparib 50 mg group, and 36 of 102 at risk in the veliparib 200 mg group. Other adverse events are listed for 78 of 101, 76 of 103, and 77 of 102 participants at risk, respectively. These are group counts from the safety record and should be read with their at-risk denominators.

The registry also lists serious adverse event terms and percentages, including malignant neoplasm progression at 15.7%, pneumonia at 7.9%, brain oedema at 4.0%, pain at 3.0%, seizure at 3.0%, and pulmonary embolism at 2.9%. The record does not specify in this summary whether these terms are presented by treatment group or the exact denominator used for each percentage, so they should not be assigned to a particular arm.

Adverse event counts describe what was recorded during the trial; they do not alone establish that a study treatment caused an event. The registry gives no death counts in the posted safety summary. A fuller assessment of safety would require context such as event timing, severity, attribution, exposure, and group-specific event details, which are not reported in this record.

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

The posted results describe a randomized comparison of two veliparib doses plus WBRT against placebo plus WBRT among adults with brain metastases from NSCLC. For overall survival, the reported medians and hazard ratios do not show a clear separation between groups. The 95% confidence intervals are broad and include the equal-hazard reference value, so the estimates do not establish a precise relative effect.

This is not the same as proving that the groups are identical. A non-significant test can occur when the true difference is small, when estimates are uncertain, or for other reasons; the posted results alone cannot distinguish all such possibilities. The registry record does not identify an equivalence or non-inferiority objective. Consequently, absence of a statistically clear difference should not be restated as evidence of equivalence.

The comparison also cannot isolate the effect of radiation. All three groups received WBRT, so the randomized contrast concerns adding veliparib rather than radiation versus no radiation. The results apply most directly to the enrolled study population and the regimens described in the registry, not automatically to other patient groups, doses, or treatment combinations.

Secondary endpoints offer additional information about response and progression, but they do not replace the primary endpoint. Their tests are subject to the same interpretive caution about uncertainty and also to the possibility of multiple comparisons, for which an adjustment is not reported. The safety counts provide descriptive context, not proof of causation or a complete comparative safety assessment.

Overall, the record supports a careful account of the estimates and their uncertainty. It does not establish that veliparib improves survival, that it has no effect, or that either dose is equivalent to placebo. Such claims would require stronger evidence and fuller details of the analysis and study context than the registry record reports.

19. Why This Trial Matters Statistically

This trial is statistically informative because it uses a randomized, double-blind, parallel-group design to compare two doses of an investigational drug against placebo while holding WBRT common across groups. Randomization supports a fairer comparison of the assigned regimens by reducing systematic differences in expectation, although it cannot eliminate uncertainty or guarantee balance in every characteristic. Double-blinding can reduce some forms of bias, but the registry record does not specify which people were masked.

The dose-ranging structure makes the two active comparisons relevant to different veliparib doses, while the shared radiation regimen helps define what the comparison can answer. It also limits the causal question: the study does not compare radiation with no radiation, and it cannot estimate a radiation effect from these arms.

The primary outcome is time-to-event, so the analysis can incorporate participants with different follow-up and censoring rather than relying only on a fixed-time survival percentage. The use of both median survival summaries and Cox-model hazard ratios gives readers complementary descriptions: one in days and one relative to the comparison group under a model. The confidence intervals are essential because they show that these estimates remain uncertain.

The trial also illustrates why a non-significant p-value is not a conclusion of equivalence. The reported estimates are near the equal-hazard reference, but their intervals include a range of plausible values. In addition, the registry does not report a complete statistical analysis plan or a multiplicity strategy for the several secondary outcomes and comparisons.

These features make the record useful for understanding how design, endpoint choice, censoring, and precision shape interpretation. They also show why estimates must be read within the randomized contrast and not expanded into claims about treatments or populations the study did not compare.

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 record gives limited detail about the trial’s original statistical design. The original sample-size justification, target power, allocation ratio, and any assumptions used when planning the study are not reported in the registry record. The planning illustrations based on observed effects are not a substitute for those original assumptions.

Although the trial is described as randomized and double-blind, the registry record does not describe the randomization sequence, concealment procedures, or which participants and staff were masked. It also does not give a full protocol or statistical analysis plan. Details of any covariate adjustment, model diagnostics, proportional-hazards assessment, or stratification for the reported analyses are not reported.

The primary endpoint description explains censoring at the last known alive date for participants not known to have died, but the record does not provide censoring counts or patterns by group. Handling of missing data for secondary outcomes is not reported. The registry also does not state whether analyses followed intention-to-treat conventions for every endpoint or how treatment discontinuation affected each analysis.

Several outcomes and comparisons are reported, but a multiplicity adjustment or formal testing sequence is not described. This limits the strength of conclusions drawn from individual secondary p-values. Some secondary confidence intervals have an unavailable upper bound in the posted record, and the reason is not reported.

The safety summary provides participant counts and a list of serious-event terms, but does not report a complete account of event timing, treatment attribution, exposure duration, or deaths. The basis for the listed serious-event percentages is not specified in this summary. These gaps constrain detailed comparisons of safety between groups.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Comparison of Veliparib and Whole Brain Radiation Therapy (WBRT) Versus Placebo and WBRT in Adults With Brain Metastases From Non-Small Cell Lung Cancer — NCT01657799.
• Registry record last updated 2018-06-06; status last verified 2018-01.
• Results first posted 2018-02-14.
• 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

NCT01657799 is a completed randomized, double-blind, parallel-group phase 2 dose-ranging study sponsored by AbbVie (prior sponsor, Abbott). It enrolled 307 adults with brain metastases from NSCLC and compared placebo, veliparib 50 mg, or veliparib 200 mg, each given with WBRT.

The primary endpoint was overall survival from randomization up to 36 months. Median survival was 185.0 days for placebo, 209.0 days for veliparib 50 mg, and 209.0 days for veliparib 200 mg. The sponsor-reported hazard ratios were close to 1, with confidence intervals including 1 and reported p-values of 0.927 and 0.906. The secondary outcomes concerned tumor response and intracranial or clinical brain metastasis progression. The record does not report a multiplicity adjustment or the trial’s original sample-size justification, so the estimates should be interpreted with attention to uncertainty and the limits of the registry entries.