Study of Cabozantinib (XL184) Versus Prednisone in Men With Metastatic Castration-resistant Prostate Cancer Previously Treated With Docetaxel and Abiraterone or MDV3100: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Cabozantinib (XL184) Versus Prednisone in Men With Metastatic Castration-resistant Prostate Cancer Previously Treated With Docetaxel and Abiraterone or MDV3100 (NCT01605227), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, controlled, parallel-group study sponsored by Exelixis. The registry lists quadruple masking. The study was designed to evaluate cabozantinib compared with prednisone for overall survival in men with previously treated metastatic castration-resistant prostate cancer. The study description specifies prior docetaxel-containing chemotherapy and abiraterone or MDV3100, and describes bone-dominant disease.

The registry lists 1028 randomized subjects: 682 assigned to cabozantinib and 346 assigned to prednisone. The cabozantinib group received placebo-matched prednisone capsules, and the prednisone group received placebo-matched cabozantinib. This matching is consistent with the listed double-blind design; the registry record does not give further detail about how masking was maintained or assessed.

The primary analysis population was Intent to Treat and included all 1028 randomized subjects. Overall survival was measured from randomization until death due to any cause. Participants who had not died or were permanently lost to follow-up were censored at their last known date alive. The registry says the analysis was performed after 614 events had occurred, with the timeframe described as approximately 24 months after study start.

The study started in 2012-07, had primary completion in 2014-09, and is listed as completed. These registry dates describe the study record; they do not establish when every participant was followed or when individual outcome observations occurred. Further details of the original sample-size justification, planned interim analyses, and complete statistical analysis plan 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent to Treat (ITT) population was used and included 1028 randomized subjects (682 cabozantinib, 346 prednisone).

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 OS was measured from the time of randomization until 614 events, approximately 24 months after study start.

The primary endpoint was overall survival, measured in months from randomization until death due to any cause. Participants who had not died or were permanently lost to follow-up were censored at the last date they were known to be alive. The registry reports median overall survival estimated with the Kaplan-Meier method and gives a 95% confidence interval for each arm. It also reports a hazard ratio from a Cox proportional hazards analysis using the Log Rank method.

Overall survival is used in time-to-event analysis because it captures how long participants remain alive after the trial’s defined starting point, while allowing follow-up times to differ. Censoring allows participants with incomplete observation to contribute information up to the time they were last known alive, rather than treating their later outcome as known. General statistical context: the Kaplan-Meier method estimates the survival pattern over time while accounting for censoring, and the median is the time at which the estimated survival probability reaches one half, if that point is observed.

The endpoint is distinct from a response measure assessed at a particular visit. It addresses time until death from any cause, not a specific cause of death or a measure of symptoms. Details about additional endpoint definitions or the handling of other forms of missing outcome data are not reported in the registry record.

7. Results Posted in the Registry

• Cabozantinib vs Prednisone: hazard ratio 0.90 (95% CI 0.76–1.06), reported p = 0.213 (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.

Bone Scan Response (BSR)

• 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:
  • Prednisone: 2.9% (10/346) versus 41.9% (286/682) on control; risk difference -39.0 percentage points (95% CI -43.1 to -34.9), risk ratio 0.07 (0.04–0.13); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Prednisone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary endpoint: bone scan response measured at the end of Week 12 as determined by the IRF. The posted secondary analysis uses the Cochran-Mantel-Haenszel method and reports a p-value below 0.001. The corresponding endpoint concerns response on a bone scan at a specified assessment, whereas the primary endpoint concerns time from randomization to death from any cause.

The secondary result therefore addresses a different aspect of the study and should be understood alongside, not in place of, the primary overall-survival analysis. The posted results show a statistical signal for the secondary endpoint while the primary hazard-ratio result has a confidence interval that includes 1 and a p-value of 0.213. This is not inherently contradictory: separate endpoints can reflect different outcomes, measurement schedules, and analysis procedures.

The registry record does not report a multiplicity-adjustment strategy for secondary testing, or enough detail to determine how the endpoint was positioned in a hierarchy of hypotheses. When multiple outcomes or analyses are examined, unadjusted p-values can overstate the strength of evidence because the chance of at least one apparently notable result can rise with the number of tests. This is a general statistical concern, not a claim about the study’s unreported analysis plan.

The secondary result can be considered supportive context, but it does not establish an effect on overall survival. Interpretation should account for the endpoint’s definition, assessment timing, analysis method, uncertainty, and the lack of reported multiplicity details. Additional secondary outcomes or their results are not reported in the registry record.

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

• Bone Scan Response (BSR)

9. Statistical Interpretation

10. Statistical Methods Explained

Overall survival is a time-to-event outcome. For each participant, the relevant observation is the interval from randomization to death or, if death was not observed, the last time the participant was known to be alive. The registry defines death due to any cause as the event. It says participants who had not died or were permanently lost to follow-up were censored at their last known date alive.

Why use Kaplan-Meier estimates?

General statistical explanation: Kaplan-Meier estimation uses observed event times and accounts for censoring, so participants who leave observation earlier can contribute information during the period they were followed. The resulting estimated survival curve describes the probability of remaining alive over time. A median survival estimate is read from that curve as the time at which the estimated probability reaches one half, when the curve reaches that level. The registry reports arm-specific medians and confidence intervals but does not provide the estimated curves’ detailed values in this discussion record.

What does censoring assume?

General statistical explanation: censoring does not mean that an unobserved event is assumed never to happen. It means that the participant’s later event time is not available, while information up to the last known observation can still be used. The validity of standard survival estimates depends on assumptions about the censoring process, including that censoring does not systematically conceal a different event pattern after accounting for the analysis. The registry describes its censoring rule but does not report diagnostics or sensitivity analyses for that assumption.

What does the hazard ratio represent?

The reported hazard ratio is 0.90 for cabozantinib versus prednisone. General statistical explanation: a hazard is the instantaneous event rate among participants still at risk at a particular time. A hazard ratio compares those rates between groups under the model and its assumptions. A ratio below 1 points toward a lower estimated hazard in the numerator group, and a ratio of 1 represents equal hazards. A hazard ratio is not a ratio of median survival times and does not directly state how many months an individual participant gains or loses.

The registry identifies the analysis parameter as Cox Proportional Hazard and the method as Log Rank. The Cox model commonly expresses the relative hazard through a hazard ratio; the Log Rank method compares event-time experience between groups. The registry does not report whether the proportional-hazards assumption was checked, whether covariates were included, or whether any adjusted model was used. No additional modeling details should be inferred from the method labels alone.

How should the p-value be read?

The reported p-value is 0.213. General statistical explanation: a p-value describes how unusual the observed data, or data more extreme, would be under a specified null hypothesis and analysis procedure. It is not the probability that the null hypothesis is true, nor does it measure the probability that a result will replicate. A p-value should be interpreted alongside the effect estimate, confidence interval, study design, and analysis assumptions. The registry does not report further detail about the exact hypothesis-testing framework beyond the listed method and result.

What information does the confidence interval add?

The 95% confidence interval for the hazard ratio is 0.76 to 1.06. General statistical explanation: a confidence interval conveys the precision of an estimate under a statistical procedure. Its width reflects uncertainty, and its endpoints identify values that are compatible with the data and procedure at the stated confidence level. It is not a range containing 95% of individual outcomes, and it does not assign a 95% probability to the fixed parameter after the data have been observed. The interval includes 1, so it includes the value corresponding to equal hazards.

The registry reports the analysis population as Intent to Treat, including all 1028 randomized subjects. This population-based approach retains participants in their randomized groups for the primary analysis. The record does not specify additional analysis populations or report the extent of missing survival information beyond its censoring description. It also does not report the original sample-size justification, the full statistical analysis plan, or planned interim analyses.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.90, and its 95% confidence interval runs from 0.76 to 1.06. The interval spans values below and above 1, the reference value for equal hazards. This means the posted estimate is not precise enough to rule out equal hazards under the reported interval procedure, and it also leaves uncertainty about the direction and size of the relative hazard. The reported p-value is 0.213.

The arm-specific median estimates also have uncertainty. Cabozantinib has a reported median of 11.0 months with a 95% confidence interval from 10.09 to 11.63 months; prednisone has a median of 9.8 months with a 95% confidence interval from 9.0 to 11.53 months. A confidence interval for each median describes uncertainty in that arm’s estimate, not a direct confidence interval for the difference between medians. The registry does not report a confidence interval for a median difference.

General statistical explanation: confidence intervals are most useful when read as ranges of estimates compatible with the data and analysis procedure, rather than as a binary significance label. Precision depends on factors such as the amount and timing of event information, censoring, and the statistical model. The record states that the primary analysis followed 614 events, but does not provide further details about event timing or censoring patterns. Consequently, the intervals and point estimates support cautious interpretation, not a claim that the true effect is exactly the reported point estimate.

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 survival planning figures are total event counts, not participants per arm. They are planning illustrations based on the observed effect and use the Schoenfeld approach. The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the total number of events required under those planning assumptions for an analysis to have an 80% chance of detecting the chosen effect at the stated significance level, if that effect and assumptions were correct. The 90% power column describes the corresponding event target for a 90% chance. These are prospective planning quantities, not guarantees about a future trial’s result.

The rows use planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects require more events to distinguish them from the null under the same assumptions. The figures therefore illustrate how strongly a planning target depends on the effect size selected; they are not a reconstruction of the original design process.

These figures are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a trial has reported results. The posted confidence interval and hazard ratio describe the trial’s result; the event targets instead show hypothetical requirements under stated planning assumptions.

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 = 0.900, so ln(HR) = -0.1054.
2. d = 4 × (1.96 + 0.842)² / [ln(0.900)]² = 2,828.2, rounded up to 2,829 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 <- 0.9                              # 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(1605227)
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 = 2,829 (80% power), 3,787 (90% power)
 75% of observed effect: events = 5,028 (80% power), 6,731 (90% power)
 50% of observed effect: events = 11,313 (80% power), 15,145 (90% power)
Simulated power with 2,829 events: 0.804 (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 4,531 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 1,028 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 <- 9.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.9          # 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: 3272        p (1-sided)   0.0001
 Events: 1277       ~HR at bound   0.8125
    Month: 17   P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.9   0.0338
    IA 2: 67%                  Z   2.5114
      N: 4532        p (1-sided)   0.0060
 Events: 2554       ~HR at bound   0.9054
    Month: 27   P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.9   0.5603
        Final                  Z   1.9930
      N: 4532        p (1-sided)   0.0231
 Events: 3830       ~HR at bound   0.9376
    Month: 60   P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.9   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 overall survival, the registry reports the sponsor’s analysis as a Cox proportional hazards result using the Log Rank method. The reported hazard ratio is 0.90, its 95% confidence interval is 0.76 to 1.06, and the p-value is 0.213. The arm-specific median estimates are also reported as Kaplan-Meier estimates.

For this time-to-event endpoint, the analysis uses the sponsor-reported hazard ratio; there is no separate recalculated hazard ratio to compare with it. A hazard ratio cannot be reconstructed from the posted medians alone because the medians do not contain the event-time information used by the survival analysis. The registry also does not provide the individual event times needed to repeat the sponsor’s analysis.

The posted summaries should therefore be interpreted as reported, with their stated analysis method and uncertainty. The confidence interval and p-value are important alongside the point estimate. Details about model diagnostics, covariate adjustment, and additional sensitivity analyses are not reported in the registry record.

16. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary overall-survival endpoint and one posted secondary endpoint, bone scan response. It gives methods and results for these analyses, but does not report whether a formal multiplicity strategy was used. It is not reported in the registry record whether secondary endpoints were tested in a prespecified hierarchy, whether p-values were adjusted, or whether any stopping or decision rules linked the endpoints.

Multiplicity matters because repeated testing can increase the chance of obtaining a nominally small p-value even when none of the tested effects is real. General statistical explanation: adjustment procedures or a prespecified testing hierarchy can help control the overall error rate, but the appropriate interpretation depends on the study’s objectives and analysis plan. Without those details, the secondary p-value should not be treated as though it necessarily had the same confirmatory status as the primary endpoint.

The primary analysis population is reported as Intent to Treat and includes all 1028 randomized subjects. For overall survival, participants who had not died or were permanently lost to follow-up were censored at their last known date alive. The registry does not report the amount of missing follow-up, the number censored, or sensitivity analyses for departures from assumptions about censoring. Details of missing-data handling for the secondary endpoint are not reported in the registry record.

The record also does not report the original sample-size justification, the full statistical analysis plan, planned interim analyses, or additional analysis populations. The primary analysis is described as having been performed after 614 events had occurred, but that alone does not establish whether interim comparisons were conducted or how any such comparisons would have been accounted for. These omissions limit assessment of prespecification and the full context for interpreting the posted p-values.

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: prostate cancer (7.9%), general physical health deterioration (7.6%), pulmonary embolism (6.2%), anaemia (4.7%), vomiting (4.1%).

The registry lists serious adverse events affecting 420 of 681 participants at risk in the cabozantinib group and 181 of 342 at risk in the prednisone group. It also lists other adverse events affecting 675 of 681 at risk in the cabozantinib group and 332 of 342 at risk in the prednisone group. These are participant counts, not estimates of a comparative treatment effect. The listed at-risk counts differ from the randomized group sizes reported for the primary analysis; the registry does not explain that difference.

The leading serious adverse-event terms listed are prostate cancer (7.9%), general physical health deterioration (7.6%), pulmonary embolism (6.2%), anaemia (4.7%), vomiting (4.1%), and pneumonia (3.5%). These entries describe the registry’s reported serious-event terms and percentages. General statistical context: adverse-event categories can overlap, so categories should not be summed unless the record establishes that they are mutually exclusive. Death counts are not reported in the registry record.

The figures alone do not establish whether an event was caused by study treatment, and they do not provide a complete comparative safety analysis. Further details such as event definitions, severity gradation, exposure duration, and adjusted comparisons are not reported in the registry record.

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

The overall-survival result is an estimated comparison between randomized groups in the population and analysis described by the registry. The reported hazard ratio is 0.90, with a 95% confidence interval from 0.76 to 1.06 and p = 0.213. The interval includes 1, so the posted result does not rule out equal hazards under the reported analysis. It also does not determine that the groups are equivalent; an interval that includes the null can still be compatible with effects in either direction.

The median estimates—11.0 months for cabozantinib and 9.8 months for prednisone—are arm-specific summaries, not a direct estimate of a median difference. They should not be read as a guarantee of how long any individual participant would live, nor as evidence that the observed median values would recur in another population. The registry’s study description limits the population to men with metastatic castration-resistant prostate cancer previously treated with docetaxel and abiraterone or MDV3100, and describes bone-dominant disease. Generalization beyond that description requires evidence not contained in the record.

The result does not establish a biological mechanism, explain why individual participants had particular outcomes, or show that the secondary bone scan response result translates into an overall-survival effect. It also does not provide a complete account of treatment harms or long-term follow-up. The serious and other adverse-event counts are descriptive registry summaries, and causal attribution is not established by those counts alone.

Statistically, the most defensible reading is that the posted estimate is uncertain and should be interpreted with its confidence interval, analysis method, population, and endpoint definition. The registry does not report the full analysis plan, multiplicity strategy, model diagnostics, or original design assumptions. Those missing details limit how completely the analysis can be evaluated, but they do not change the numerical results that the record reports.

19. Why This Trial Matters Statistically

This trial provides a useful example of how a time-to-event result should be read beyond its point estimate. The hazard ratio is accompanied by a confidence interval and p-value, while the registry also reports Kaplan-Meier median estimates for each randomized group. These quantities answer related but distinct questions: the medians summarize each group’s estimated survival distribution at a point, while the hazard ratio compares event rates over follow-up under its model assumptions.

The result illustrates why statistical interpretation should not be reduced to whether a p-value crosses a threshold. The point estimate’s direction, the interval’s width and position relative to 1, the endpoint, and the analysis population all contribute to interpretation. Here, the confidence interval includes 1, and the reported p-value is 0.213; the point estimate alone is not enough to characterize the evidence.

The posted secondary endpoint also illustrates that different outcomes can yield different statistical findings. A response measure assessed at a particular time is not interchangeable with overall survival. The distinction matters when considering multiple endpoints, especially because the registry does not report a multiplicity strategy.

Finally, the record allows readers to distinguish reported findings from missing methodological context. It identifies the randomized design, masking, primary analysis population, censoring rule, and event-based analysis timing, while leaving some design and analysis details unreported. Recognizing both the available information and its limits is central to sound interpretation of clinical trial statistics.

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 gives the main overall-survival estimates and the stated analysis method, but it does not report the full statistical analysis plan. Model diagnostics, including assessment of the proportional-hazards assumption, are not reported. The hazard ratio’s interpretation depends on the model and its assumptions, so the absence of those details limits independent evaluation of that analysis.

The record states that the primary analysis followed 614 events, but it does not provide the event timing or detailed censoring pattern. It describes censoring for participants who had not died or were permanently lost to follow-up, yet does not report the number censored or sensitivity analyses for missing follow-up. The original sample-size justification and any interim-analysis plan are not reported in the registry record.

The registry lists one secondary endpoint and its analysis result, but does not report a multiplicity strategy or a hierarchy of endpoints. This makes it difficult to assess the intended inferential status of the secondary result. The record also does not report additional secondary endpoint results, so the posted secondary findings may not represent the full set of outcomes assessed in the study.

Safety summaries include participant counts and leading serious-event terms, but the registry does not report details needed for a full comparative safety assessment, such as exposure-adjusted analyses or causal attribution. Death counts are not reported in the registry record. The record’s safety at-risk counts also differ from the randomized group counts, without an explanation for the difference.

Finally, a registry summary cannot replace detailed outcome definitions, participant-level data, or the complete analysis documentation. These limitations do not invalidate the posted estimates, but they constrain conclusions about assumptions, missing information, and the broader context of the analyses.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Cabozantinib (XL184) Versus Prednisone in Men With Metastatic Castration-resistant Prostate Cancer Previously Treated With Docetaxel and Abiraterone or MDV3100 — NCT01605227.
• Registry record last updated 2018-03-14; status last verified 2018-02.
• Results first posted 2018-03-14.
• 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

NCT01605227 is a completed Phase 3, randomized, double-blind, controlled, parallel-group study sponsored by Exelixis. It compared cabozantinib with prednisone in men with metastatic castration-resistant prostate cancer previously treated with docetaxel and abiraterone or MDV3100. The registry lists 1028 randomized subjects, with 682 assigned to cabozantinib and 346 to prednisone.

The primary endpoint was overall survival. The registry reports medians of 11.0 months and 9.8 months, respectively, and a hazard ratio of 0.90 with a 95% confidence interval from 0.76 to 1.06 and p = 0.213. The primary analysis used the Intent to Treat population and followed 614 events. One secondary endpoint, bone scan response, is posted. Several design and analysis details, including the original sample-size justification and multiplicity strategy, are not reported in the registry record.