Study of Cabozantinib (XL184) vs Placebo in Subjects With Hepatocellular Carcinoma Who Have Received Prior Sorafenib: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Cabozantinib (XL184) vs Placebo in Subjects With Hepatocellular Carcinoma Who Have Received Prior Sorafenib (NCT01908426), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

The study evaluated an active drug against placebo in people whose hepatocellular carcinoma had been treated previously with sorafenib. Its primary endpoint was overall survival (OS), a time-to-event outcome that records how long participants remain alive after randomization. The registry also reports progression-free survival (PFS), another time-to-event outcome, and objective response rate (ORR), a count of participants meeting the response outcome.

The clinical question is comparative rather than a claim about an individual participant. The registry reports group-level estimates and uncertainty for the primary outcome, along with results for the secondary outcomes. Those estimates describe the randomized groups and do not establish what would happen for a particular person. They also do not, by themselves, describe the balance of potential benefits and harms for an individual.

The posted results concern the study population and the follow-up described in the registry record. They should be read in the context of prior sorafenib treatment and the trial's placebo comparison; they do not directly answer questions about other populations, other comparators, or treatment sequences not studied in this record.

3. Trial Design

This was a phase 3, randomized, double-blind, controlled study with a parallel-group model. The registry lists quadruple masking. It does not report which specific groups of people were masked under that label. The study was sponsored by Exelixis and is recorded as completed. The registry lists a start date of 2013-09-26 and a primary completion date of 2017-10-16.

The registry records enrollment of 707 randomized subjects. The primary interim analysis population included 707 subjects: 470 assigned to cabozantinib and 237 assigned to placebo. Cabozantinib was given as a 60 mg tablet once daily; the comparator was an oral cabozantinib-matched placebo tablet once daily. The allocation procedure beyond randomization, including the method used to generate and conceal the allocation sequence, is not reported in the registry record.

The primary endpoint was OS, defined as time from randomization to death from any cause. The stated timeframe was up to 45 months. The analysis used Kaplan-Meier estimates and the ITT population. The primary analysis was based on a second planned interim analysis, prespecified to occur at approximately the 75% information fraction, described in the registry as approximately 466 deaths. The data cutoff for this event-driven analysis was 01 June 2017.

PFS and ORR were listed as secondary outcomes. PFS was measured over up to 45 months. ORR was assessed radiologically every 8 weeks after randomization until disease progression or discontinuation of study treatment, up to 45 months. The registry record does not report the trial's original sample-size justification or the 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:

Analysis population for the primary outcome, as defined in the registry: The ITT population was used and included 707 randomized subjects (470 cabozantinib, 237 placebo) in the second interim analysis with a cutoff date of 01 June 2017.

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 (OS), measured over Up to 45 months.

Overall survival measures the time from randomization until death from any cause. It is a time-to-event endpoint: the outcome includes both whether the event occurred and when it occurred. In this study, the registry reports the median OS for each randomized group and the sponsor's hazard-ratio comparison. The stated timeframe was up to 45 months, and the primary analysis used Kaplan-Meier estimates.

OS is used in clinical trials because death is a direct, clearly defined event and does not require an assessment of tumor response to determine whether the event occurred. Measuring from randomization also anchors the comparison at a shared point in the trial. The definition includes death from any cause rather than only deaths attributed to the cancer or study treatment.

The median is the time by which the Kaplan-Meier estimate indicates that half of the group has experienced the event. It is not the average survival time, and it does not describe every participant's experience. A hazard ratio summarizes the relative event rate over follow-up, rather than comparing the two median times as a simple ratio. Its interpretation depends on the time-to-event analysis and should be considered with its confidence interval.

The registry does not report detailed information about censoring rules or the handling of missing follow-up in the OS analysis. These details matter because time-to-event estimates rely on follow-up information for participants who have not had the event by the time their observation ends.

7. Results Posted in the Registry

• Cabozantinib (XL184) vs Placebo: hazard ratio 0.76 (95% CI 0.63–0.92), reported p = 0.005 (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.

Progression-Free Survival (PFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Cabozantinib (XL184) vs Placebo: hazard ratio 0.44 (95% CI 0.36–0.52), 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 Cabozantinib (XL184) vs Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Objective Response Rate (ORR)

• 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:
  • Cabozantinib (XL184): 3.8% (18/470) versus 0.4% (1/237) on control; risk difference 3.4 percentage points (95% CI 1.5 to 5.3), risk ratio 9.08 (1.22–67.58); unadjusted two-proportion z-test p = 0.008.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cabozantinib (XL184) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide evidence on tumor progression and response alongside the primary survival outcome. The registry reports PFS as a time-to-event endpoint and ORR as a participant-count endpoint. The sponsor-reported comparisons favor the cabozantinib group in direction for both outcomes, consistent with the direction of the primary OS comparison. They address related but different aspects of the trial, so they should not be treated as interchangeable confirmations of the same outcome.

PFS concerns the timing of progression-free survival events, while ORR concerns radiologic response as assessed during follow-up. Neither endpoint is itself a direct measure of overall survival. The secondary results can help describe the pattern across outcomes, but they cannot establish that changes in those outcomes account for the OS result or that the outcomes have the same clinical importance.

Secondary analyses generally carry less inferential weight when the registry does not report how multiplicity was handled. Testing several outcomes can increase the chance of at least one apparently positive result by chance if each is interpreted without adjustment. The registry identifies PFS and ORR as secondary outcomes, but does not report an overall multiplicity procedure or a hierarchy for interpreting them. Their p-values should therefore be read as the reported endpoint-specific results, not as proof that a family-wide error rate was controlled.

The ORR sponsor test and the unadjusted recalculation also differ in method. That distinction is important when placing the outcomes together: the sponsor's reported test remains the trial analysis, while the simple calculation is supplementary. The registry does not report a multiplicity-adjusted interpretation for the secondary outcomes, so the secondary pattern is informative but less conclusive than a primary endpoint result supported by a prespecified testing plan.

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

• Progression-Free Survival (PFS)
• Objective Response Rate (ORR)

9. Statistical Interpretation

10. Statistical Methods Explained

The methods below explain the statistical quantities in general terms and how they relate to the registry's reported analyses. The registry identifies Kaplan-Meier estimates for median OS and Log Rank methods for the reported hazard ratios. It identifies a Cochran-Mantel-Haenszel method for the sponsor's ORR comparison. More detailed specifications of these procedures are not reported in the registry record.

What does a median time-to-event estimate describe?

For a time-to-event outcome, each participant contributes information about the time from a defined starting point until an event, or until follow-up ends without the event being observed. Kaplan-Meier estimation uses that event-time information to estimate the probability of remaining event-free over time. The median is the time at which the estimated event-free probability reaches one half. It describes the middle of the estimated distribution, not an average and not a guarantee about an individual participant's outcome.

In OS, the event is death from any cause and the time origin is randomization. In PFS, the registry names progression-free survival as the outcome, but the precise event definition and assessment rules are not reported in the registry record. Time-to-event results are affected by how follow-up is handled when an event has not been observed; detailed censoring and missing-follow-up procedures are not reported for these outcomes.

What does a hazard ratio convey?

A hazard is the event rate at a particular time among participants who have not yet experienced the event. A hazard ratio compares those rates between groups over the analysis. In general, a value below 1 means the estimated hazard is lower in the first-named group than in the comparator group; it is not a ratio of medians or a difference in months. A single hazard ratio is a compact summary of the time-to-event comparison. Its interpretation can be less straightforward if the relative hazards vary over time. The registry record does not report a proportional-hazards assessment or other detail about whether that assumption was examined.

The Log Rank test compares event-time patterns between groups while accounting for the ordering of observed event times. The registry reports this method for the OS and PFS comparisons. It does not report the full model specification, covariate adjustments, or stratification factors for those analyses. The hazard ratios are sponsor-reported results and should be read with their confidence intervals rather than as isolated point estimates.

How should a confidence interval be read?

A confidence interval communicates uncertainty around an estimate under the statistical procedure used. A narrower interval indicates greater precision than a wider interval on the same scale, while neither interval guarantees that the true effect lies within its endpoints. For hazard ratios, the null value is 1; for a difference, the null value is 0. An interval that includes the null value is compatible with no difference at the confidence level used, though it does not prove that there is no effect. The registry reports 95% confidence intervals for the primary and PFS hazard ratios and for the OS and PFS medians.

Why can event counts matter?

Time-to-event analyses draw much of their information from the number and timing of events, not just the number enrolled. A planning calculation for a time-to-event comparison can therefore be expressed in total events. The registry's planning illustration uses the Schoenfeld approach for those outcomes. Its event totals are planning quantities under stated assumptions; they are not the observed number of deaths in the primary analysis, nor a substitute for the sponsor's analysis.

What is different about the ORR analysis?

ORR is reported as a count of participants, rather than a median follow-up time. The registry describes radiologic assessment every 8 weeks after randomization until progression or discontinuation of study treatment, up to 45 months. The sponsor's reported test is Cochran-Mantel-Haenszel, with a p-value but no reported effect estimate or confidence interval in that analysis record. The test can compare groups across strata, but the strata used in this trial are not reported in the registry record.

A separate simple, unadjusted calculation based on the posted group counts gives a risk difference and an unadjusted p-value. Such a calculation is not interchangeable with a sponsor analysis using a different stated method. The registry record does not report details that would explain the exact analytical choices behind the sponsor's test, so the sponsor's named method and result should be kept distinct from an unadjusted recalculation.

What does over-dispersion mean in general?

For count outcomes, over-dispersion means that observed variability exceeds what a particular statistical model expects. It can make standard errors too small if the extra variability is ignored. The registry does not report an over-dispersion assessment or a count model for the outcomes. This general issue should not be mistaken for a finding about this trial.

11. Confidence Intervals and Precision

The primary OS hazard ratio is 0.76, with a 95% confidence interval of 0.63 to 0.92. This interval conveys uncertainty about the relative hazard under the sponsor's analysis. It lies below the null value of 1, but it still spans a range of possible relative effects; the point estimate should not be read as an exact or universal effect.

The median OS estimate for cabozantinib is 10.2 months, with a 95% confidence interval of 9.1 to 12.0 months. The placebo median is 8.0 months, with a 95% confidence interval of 6.8 to 9.4 months. These intervals express uncertainty in each median estimate. They are not a confidence interval for the difference between medians, and their overlap is not a substitute for the reported comparison test.

The PFS hazard ratio is 0.44, with a 95% confidence interval of 0.36 to 0.52. The interval is narrower on the hazard-ratio scale than the OS interval, but precision should be considered in relation to the outcome and analysis as well as interval width. The placebo PFS median is reported as 1.9 months, with both confidence limits also at 1.9 months. Identical rounded endpoints do not show the underlying unrounded estimate or explain the precision of that result.

The ORR sponsor analysis reports a p-value but no confidence interval for an effect estimate. Consequently, the sponsor-reported ORR result does not convey uncertainty on a directly interpretable effect scale in that analysis record. The separate unadjusted recalculation has a risk-difference interval, but it is not a replacement for the sponsor's named test.

Confidence intervals do not include every source of uncertainty. They do not address unreported design details, missing-data procedures, analysis choices, or generalizability to populations not enrolled in the trial.

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 are based on the observed effect and are not the original trial design calculations. The original design assumptions and sample-size justification are not reported in the registry record. For OS and PFS, the displayed planning quantities are total events, calculated using the Schoenfeld approach. For ORR, they are participants per arm.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The event-based calculations concern total events; they should not be interpreted as the total number of participants to enroll. The ORR figures are participants per arm, not a combined sample size.

The 80% power column describes the planning number of events or participants under which the calculation would have an 80% chance of rejecting the null hypothesis if the chosen effect were the true effect and the assumptions held. The 90% column uses a higher probability of detecting that effect under the same planning framework. These are hypothetical design properties, not properties measured after the trial.

The rows that plan for 100% of the observed effect use the full observed estimate as the target. Rows planning for 75% or 50% of the observed effect target smaller effects. Smaller effects are harder to distinguish from chance variation, so the planning calculations require more events or participants. These illustrations do not establish the probability that the completed trial detected an effect, and they are not observed power.

For a real design, the assumptions would need to reflect the intended population, analysis, outcome frequency or event process, and acceptable error rates. The registry does not report whether these illustrative assumptions match the decisions used when the trial was designed.

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 = 0.760, so ln(HR) = -0.2744.
2. d = 4 × (1.96 + 0.842)² / [ln(0.760)]² = 416.9, rounded up to 417 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 <- 0.76                              # 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(1908426)
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 = 417 (80% power), 559 (90% power)
 75% of observed effect: events = 742 (80% power), 993 (90% power)
 50% of observed effect: events = 1,668 (80% power), 2,233 (90% power)
Simulated power with 417 events: 0.795 (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 653 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 707 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 <- 8          # control-arm median, months (converted from the posted unit)
hr          <- 0.76          # 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: 454         p (1-sided)   0.0001
 Events: 188        ~HR at bound   0.5819
   Month: 17    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.76   0.0338
   IA 2: 67%                   Z   2.5114
      N: 654         p (1-sided)   0.0060
 Events: 376        ~HR at bound   0.7717
   Month: 26    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.76   0.5603
       Final                   Z   1.9930
      N: 654         p (1-sided)   0.0231
 Events: 564        ~HR at bound   0.8454
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.76   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 sponsor-reported OS analysis gives a hazard ratio of 0.76, a 95% confidence interval of 0.63 to 0.92, and p = 0.005 using the Log Rank method. The posted primary result and reported analysis agree on those values. The sponsor's own analysis is the main inferential result to retain for OS; the registry does not flag a discrepancy for that endpoint.

For PFS, the sponsor reports a hazard ratio of 0.44, a 95% confidence interval of 0.36 to 0.52, and p < 0.001, also using Log Rank. These are the reported time-to-event results, rather than a simple recalculation from the displayed medians.

For ORR, the sponsor reports a Cochran-Mantel-Haenszel test with p = 0.009. A separate recalculation from the posted counts is unadjusted and gives p = 0.008. These values arise from different analysis approaches; the recalculated value should not be substituted for the sponsor's test. The registry record does not provide enough detail about the sponsor's stratification or other analytical specifications to reconcile the values further. The simple recalculation is descriptive support, not a replacement for the prespecified sponsor analysis.

16. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary OS endpoint and two secondary outcomes, PFS and ORR. It also states that OS was analyzed at a second planned interim analysis at approximately the 75% information fraction, described as approximately 466 deaths. The data cutoff was 01 June 2017. This describes the timing and event-driven basis of the posted primary analysis, but it does not provide the complete interim-monitoring plan.

The registry record does not report whether statistical significance thresholds were adjusted for interim analyses, what stopping boundaries may have been used, or how repeated testing was handled. It also does not report a multiplicity adjustment or testing hierarchy across the primary and secondary outcomes. Without those details, the p-values should be read as reported for their named analyses, not as evidence that a particular family-wise error rate was maintained.

The primary OS analysis used the ITT population. The registry describes that population as including all 707 randomized subjects in the second interim analysis, with the group counts recorded as 470 for cabozantinib and 237 for placebo. Use of an ITT population generally preserves the randomized-group comparison by analyzing participants according to assignment. The registry does not report how missing outcome data, withdrawals, or incomplete follow-up were handled in practice.

For PFS, the outcome measure records a median and hazard ratio, but the detailed endpoint definition and missing-data rules are not reported in the registry record. For ORR, the registry describes the assessment schedule and reports group counts, but does not state how participants without an evaluable radiologic assessment were treated in the analysis. It also does not report the strata used for the Cochran-Mantel-Haenszel test.

These omissions do not invalidate the reported results, but they limit independent evaluation of the full analysis strategy. The reported endpoint estimates and methods can be described; decisions about multiplicity, censoring, missing observations, and analysis populations beyond the stated ITT population cannot be reconstructed from the registry record.

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: hepatocellular carcinoma (9.3%), abdominal pain (3.8%), general physical health deterioration (3.6%), pneumonia (3.4%), hepatic failure (3.4%).

The registry lists serious adverse event counts for the groups and identifies the number at risk for those summaries. For cabozantinib, 232 serious adverse events are reported among 467 at risk; for placebo, 87 are reported among 237 at risk. The record also reports 445 other adverse events among 467 at risk in the cabozantinib group and 173 among 237 at risk in the placebo group. These are event-summary counts, not estimates of comparative risk adjusted for follow-up or participant characteristics.

The registry reports deaths of 314 in the cabozantinib group and 167 in the placebo group. Those counts should be read in the context of the group sizes and time-to-event follow-up; they do not, alone, provide a causal assessment or a comparison adjusted for time at risk. The OS analysis uses death from any cause as its endpoint, but the adverse-event listing does not establish the cause of each death.

The most frequently listed serious adverse event terms include hepatocellular carcinoma at 9.3%, abdominal pain at 3.8%, general physical health deterioration at 3.6%, pneumonia at 3.4%, hepatic failure at 3.4%, and hepatic encephalopathy at 3.2%. These terms describe reported events in the record. Counts and percentages do not establish that the study treatment caused an event, and they do not fully characterize severity, timing, duration, or attribution.

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

The posted primary result is a group-level comparison of OS in a randomized study of cabozantinib and placebo among people with hepatocellular carcinoma who had received prior sorafenib. The reported hazard ratio is below 1, its 95% confidence interval is also below 1, and the sponsor reports p = 0.005. These statistics indicate evidence of a difference in the analyzed groups under the stated method, with uncertainty about the effect's size.

The result does not mean that every participant in the cabozantinib group lived longer than every participant in the placebo group. The median estimates describe the distributions for the groups, not individual outcomes. The hazard ratio summarizes relative event rates over follow-up and is not a direct ratio of survival times. Nor does a statistically significant result by itself establish that the magnitude is clinically important.

The findings are specific to the population, treatment comparison, endpoints, and follow-up recorded in this trial. They do not establish outcomes for people with a different clinical history, for comparisons with treatments other than placebo, or for treatment strategies not studied in the registry record. The trial is recorded as completed, but that status does not add details about analyses that are not reported.

The secondary results add information about progression and response, but they do not change the definition of the primary endpoint. Their interpretation is limited by the absence of reported multiplicity procedures and by the fact that the ORR sponsor analysis does not provide an effect estimate with a confidence interval in the analysis record. The unadjusted recalculation is not a substitute for that analysis.

Finally, effectiveness and safety are separate parts of interpretation. The adverse-event summaries record events and deaths but do not, by themselves, show causation or provide a complete comparative safety assessment. A balanced judgment would require the full clinical context and analysis details, some of which are not reported in the registry record.

19. Why This Trial Matters Statistically

This trial illustrates why a primary endpoint and its analysis method need to be read together. OS is defined from randomization to death from any cause, and the registry reports both group medians and a sponsor-reported hazard ratio. The median gives an interpretable time point in each estimated distribution; the hazard ratio summarizes the comparative time-to-event pattern. They answer related but different statistical questions.

The interim nature of the primary analysis is also important. The registry describes a second planned interim analysis at approximately the 75% information fraction, or approximately 466 deaths, with a cutoff date of 01 June 2017. Event-driven analyses make the distinction between enrollment and accumulated endpoint events visible: information in a survival analysis depends on observed event experience, not enrollment alone. The full monitoring plan is not reported, so the interim result cannot be evaluated against unreported stopping rules.

The secondary outcomes show why endpoint families require careful interpretation. PFS, ORR, and OS do not measure the same thing, and multiple analyses raise questions about multiplicity. The registry gives endpoint-specific results but does not state how the secondary tests were organized or adjusted. A statistically notable secondary result therefore deserves a different level of confidence from a primary result with a clearly described analysis plan.

Finally, the record contrasts sponsor-reported analyses with a simple unadjusted recalculation for ORR. That comparison demonstrates why method matters: a p-value is tied to the test that generated it, and results from distinct procedures should not be treated as interchangeable. Clear separation of reported analyses, recalculations, uncertainty, and missing methodological details supports more careful interpretation.

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.

Several trial-specific details needed for a complete assessment are not reported in the registry record. These include the original sample-size justification, the full statistical analysis plan, the randomization and allocation-concealment procedures, and which people were masked under the quadruple-masking label. The registry identifies an interim OS analysis but does not report its monitoring boundaries or any adjustment for interim testing.

The record does not report the detailed censoring rules or handling of missing follow-up for OS and PFS. It names PFS but does not provide the full event definition or assessment rules. The ORR assessment schedule is stated, but the handling of participants without an evaluable assessment is not reported. The strata used for the sponsor's Cochran-Mantel-Haenszel analysis are also not stated.

The primary analysis is based on a cutoff date rather than complete follow-up for every participant. The registry describes the analysis as event-driven and reports the planned information fraction, but it does not provide participant-level follow-up distributions or additional detail about how observation ended for participants without an event. These constraints make it difficult to assess the effect of follow-up patterns independently.

The ORR sponsor result provides a p-value but no sponsor-reported effect estimate or confidence interval in the analysis record. The simple unadjusted recalculation is not the same analysis and should not be taken as a replacement. Across secondary outcomes, the absence of a reported multiplicity strategy limits the strength of conclusions drawn from endpoint-specific p-values. These are limitations in what can be established from the registry record, not claims that the underlying study necessarily lacked such procedures.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Cabozantinib (XL184) vs Placebo in Subjects With Hepatocellular Carcinoma Who Have Received Prior Sorafenib — NCT01908426.
• Registry record last updated 2021-05-06; status last verified 2021-04.
• Results first posted 2019-03-01.
• 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 record describes a completed phase 3 randomized, double-blind, controlled, parallel-group study comparing cabozantinib (XL184) with placebo in people with hepatocellular carcinoma who had received prior sorafenib. It records 707 randomized subjects and lists OS as the primary outcome, with PFS and ORR as secondary outcomes.

The primary OS analysis used the ITT population and Kaplan-Meier estimates, with a second planned interim analysis and data cutoff of 01 June 2017. The sponsor-reported OS hazard ratio was 0.76, with a 95% confidence interval of 0.63 to 0.92 and p = 0.005. The registry also reports secondary endpoint analyses and adverse-event summaries.

The record does not report the full statistical analysis plan, original sample-size justification, or several details needed to assess multiplicity and missing-data handling. Interpretation should distinguish sponsor-reported analyses from unadjusted recalculations and should retain the uncertainty and population limits of the posted results.