Study of Cabozantinib (XL184) Versus Mitoxantrone Plus Prednisone in Men With Previously Treated Symptomatic Castration-resistant Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Cabozantinib (XL184) Versus Mitoxantrone Plus Prednisone in Men With Previously Treated Symptomatic Castration-resistant Prostate Cancer (NCT01522443), a randomized phase 3 study. The primary outcome is Pain Response at Week 6 Confirmed at Week 12, Week 12 Reported.

2. Clinical Question

The study addressed pain response and bone-scan response in men with castration-resistant prostate cancer. The registry describes bone metastases and associated pain as an important clinical problem in this population, and states that the study evaluated cabozantinib versus mitoxantrone plus prednisone on pain response and bone-scan response. Those stated aims describe the question being investigated; they do not establish a treatment effect.

The primary endpoint was a binary measure: participants either met the defined pain-response criteria or did not. The posted primary outcome reports the percentage of responders at Week 12. The central comparison is therefore between the observed responder proportions in the two randomized arms, alongside the uncertainty around those estimates and the registry-reported statistical test.

3. Trial Design

This was a randomized, phase 3, parallel-group trial comparing cabozantinib with mitoxantrone plus prednisone. The registry lists quadruple masking. The planned treatment groups were cabozantinib and mitoxantrone plus prednisone, with matching placebos described for the other arm’s treatment components. The registry record does not report further details about how masking was maintained or assessed.

Enrollment was 119 participants. The primary analysis population was the Intent to Treat population, with 61 participants in the cabozantinib arm and 58 in the mitoxantrone plus prednisone arm. The trial record lists pain response as the primary outcome and bone scan response and overall survival as secondary outcomes. Pain was assessed by participant self-report at Week 6 and Week 12; bone scan response was assessed at the end of Week 12 by the IRF. Overall survival was measured from randomization until 78 deaths.

The record lists a start date of 2012-03 and primary completion in 2014-10. Its status is terminated. The reason for termination is not reported in the registry record, and the status alone does not establish why the study ended or what effect the status had on follow-up or analysis. The original design’s sample-size justification and planned statistical assumptions are not reported in the registry record.

Randomization supports a comparison between assigned groups, but it does not remove uncertainty from the small number of participants or guarantee that all potential sources of bias were controlled. The posted results should be interpreted in light of the endpoint definitions, the reported analysis methods, and the missing information about analysis procedures.

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 primary analysis of pain response was based on the Intent to Treat (ITT) population of 119 participants (61 cabozantinib, 58 mitoxantrone plus 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 Pain Response at Week 6 Confirmed at Week 12, Week 12 Reported, measured over Pain response was measured at Week 6 and Week 12 by self-reports of subjects.

The primary endpoint was pain response at Week 6 confirmed at Week 12, with the Week 12 result reported. Pain response required a reduction of at least 30% from baseline in average daily worst pain intensity during a 7-day reporting period. The response definition also required no concomitant increase in average daily use of any opioid narcotic type and no addition of a new opioid narcotic type relative to baseline.

The endpoint combines a participant-reported pain measure with opioid-use conditions. This matters because a decrease in reported pain alone would not meet the stated response definition if opioid use increased in the specified ways. The registry also defines pain progression using an increase of at least 30% in average daily worst pain intensity, an increase in average daily use of any opioid narcotic type, or addition of a new opioid type relative to baseline.

As a binary outcome, the endpoint expresses the proportion meeting the response criteria rather than the size of each participant’s change in pain. This kind of measure can make a clinically interpretable responder comparison, while also discarding detail about the range of changes among responders and nonresponders. The registry identifies the outcome as the prespecified primary analysis, but does not report the rationale for selecting this particular threshold or further details about how incomplete pain reports were handled.

7. Results Posted in the Registry

• Mitoxantrone/Prednisone: 17.2% (10/58) versus 14.8% (9/61) on control; risk difference 2.5 percentage points (95% CI -10.7 to 15.7), risk ratio 1.17 (0.51–2.67); unadjusted two-proportion z-test p = 0.711.

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:
  • Mitoxantrone/Prednisone: 5.2% (3/58) versus 31.1% (19/61) on control; risk difference -26.0 percentage points (95% CI -38.9 to -13.0), risk ratio 0.17 (0.05–0.53); 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 Mitoxantrone/Prednisone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Survival (OS)

• 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 vs Mitoxantrone/Prednisone: hazard ratio 0.70 (95% CI 0.44–1.10), reported p = 0.121 (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 Cabozantinib vs Mitoxantrone/Prednisone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the study’s assessment beyond the primary self-reported pain-response measure. Bone scan response concerns a different aspect of disease assessment, while overall survival is a time-to-event outcome. Together, they address distinct questions, so their results should be considered alongside, rather than substituted for, the primary endpoint.

The posted bone scan result has a statistically significant registry-reported comparison, whereas the overall survival comparison is not statistically significant. This pattern does not resolve the primary pain-response question. A difference in a secondary endpoint can coexist with an inconclusive primary comparison because the endpoints measure different outcomes and have different statistical properties.

Secondary outcomes often involve multiple comparisons. In general, examining multiple outcomes can increase the chance that at least one result appears statistically notable by chance if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity adjustment or testing hierarchy. Accordingly, unadjusted secondary results carry less weight as confirmatory evidence than a prespecified primary analysis with a stated testing strategy. The record does not report whether such a strategy existed outside the posted registry information.

The secondary findings can therefore be treated as descriptive and hypothesis-generating in this record, with their own estimates and uncertainty considered separately. They do not provide a basis for changing the interpretation of the primary endpoint or for asserting a comprehensive treatment effect across all outcomes.

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

• Bone Scan Response (BSR)
• Overall Survival (OS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a binary outcome, because each participant is classified as meeting or not meeting the prespecified pain-response definition. The arm-level percentages estimate the proportion of participants classified as responders. A confidence interval around each percentage conveys the statistical uncertainty in estimating that proportion from the participants observed in that arm.

What does the primary comparison test?

The registry reports a Cochran-Mantel-Haenszel analysis for the primary comparison. In general, this method compares outcomes across groups while accounting for specified strata. The registry record does not identify the strata used for this analysis, so the details of any stratification cannot be described. The reported p-value is 0.773. In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the test; it is not the probability that the null hypothesis is true and does not measure the size or importance of an effect.

A recalculated unadjusted comparison is also available. It uses the posted summary counts and compares the observed responder proportions without the registry-reported stratified method. Its p-value is 0.711. The recalculated result is not a substitute for the registry-reported analysis, because the two analyses use different methods. The registry does not report the strata or additional model details needed to reproduce the Cochran-Mantel-Haenszel analysis from the record alone.

How should confidence intervals be read?

In general, a confidence interval is a range generated by a statistical procedure that, under its assumptions, has a stated long-run coverage rate for the quantity being estimated. The posted arm-specific intervals represent uncertainty around each response percentage. A comparison of arm-specific intervals is not the same as a confidence interval for the treatment contrast. For assessing the contrast, the interval around the difference or the registry-reported test is more directly relevant. The registry-reported primary analysis does not post an effect estimate or confidence interval for its Cochran-Mantel-Haenszel comparison.

The unadjusted recalculation reports a risk difference and interval, but the registry analysis remains the prespecified reported analysis. Because the recalculation is unadjusted, it should be understood as a simple comparison of posted summary data rather than as a reconstruction of all features of the trial’s analysis plan.

What do the secondary analysis methods contribute?

For bone scan response, the registry also reports a Cochran-Mantel-Haenszel comparison and a p-value below 0.001. The simple unadjusted recalculation likewise reports p < 0.001. The registry does not report the stratification details for this analysis. For overall survival, the registry reports a log-rank analysis and a hazard ratio of 0.70, with a 95% confidence interval from 0.44 to 1.10 and p = 0.121.

In general, the log-rank test compares the time-to-event experience of groups over follow-up. A hazard ratio summarizes the relative event rates over time under the model and interpretation used for that analysis; it is not a ratio of median survival times. The overall survival outcome is described as measured from randomization until 78 deaths. Further details about censoring, the analysis population, or model checks are not reported in the registry record.

Median survival is a descriptive summary of the time-to-event distribution. It does not capture every feature of the survival curves, and a difference between medians alone would not provide a complete comparison. The reported hazard ratio and its confidence interval are more directly tied to the registry’s log-rank comparison, but the interval includes values on both sides of 1.00, and the reported p-value is not statistically significant at conventional levels.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation is greater than a statistical model assumes. If a method assumes less variation than is actually present, standard errors can be too small and confidence intervals too narrow. The posted primary and bone scan endpoints are binary, and the registry does not report a model for over-dispersion or indicate that it was assessed. This is a general statistical consideration, not a reported feature of this trial’s analysis.

For these results, the most important methodological distinction is between the registry-reported analyses and simple unadjusted recalculations from the posted summary statistics. The registry’s primary analysis is the Cochran-Mantel-Haenszel test; the recalculated primary p-value comes from an unadjusted comparison. They answer related but not identical analytic questions. Neither p-value alone establishes equivalence, and the reported uncertainty should be considered alongside the observed response percentages.

11. Confidence Intervals and Precision

The arm-specific 95% confidence intervals for pain response are broad: 5.9% to 24.0% for cabozantinib and 7.5% to 27.0% for mitoxantrone plus prednisone. They overlap, and each interval covers a range of plausible response percentages under the method’s assumptions. The point estimates are 15.0% and 17.0%, respectively. Because the estimates come from 61 and 58 participants, the data provide limited precision for distinguishing modest differences between the arm-level response proportions.

These arm-specific intervals should not be read as an interval for the difference between treatments. The unadjusted recalculation includes an interval for the risk difference, but it is a simple unadjusted estimate rather than the interval from the registry-reported Cochran-Mantel-Haenszel analysis. The registry record does not report a confidence interval for its primary adjusted comparison.

For bone scan response, the reported arm-specific intervals are 20.0% to 43.0% for cabozantinib and 0.0% to 11.0% for mitoxantrone plus prednisone. For overall survival, the median estimates have reported confidence intervals of 6.8 to 11.56 months and 5.26 to 9.1 months, respectively. The hazard-ratio confidence interval extends from 0.44 to 1.10. These intervals have different meanings because they relate to different outcome measures.

In general, wider intervals indicate less precision, while narrower intervals indicate more precision under the analysis assumptions. Precision is not the same as absence of bias, and confidence intervals do not account for every uncertainty, including unreported missing-data or analysis choices.

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 use the observed effect as a starting point and show examples for detecting the full observed effect, 75% of that effect, and 50% of that effect. For binary outcomes such as pain response and bone scan response, the displayed figures are participants per arm. For overall survival, the figures are total events, not participants per arm or total enrollment.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is the stated fraction of the observed effect. The registry record does not report the original trial’s sample-size justification or original design assumptions, so these illustrations should not be interpreted as the trial’s own planning calculations.

The 80% power column describes the number of participants per arm for a binary outcome, or total events for a time-to-event outcome, that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions. The 90% power column gives the corresponding planning quantity for a 90% chance. Greater target power generally requires more information. Smaller target effects also require more participants or events to distinguish them from no effect, all else equal.

These figures are planning illustrations based on the observed effect, not observed power. They do not indicate the probability that the trial’s results are correct, and they do not determine whether the original trial was adequately designed. The original design rationale is not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.148; treatment proportion p₁ = 0.172; average p̄ = 0.160.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5184 = 1.0161.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5181 = 0.4361.
4. n = (1.0161 + 0.4361)² / (0.0249)² = 3,408.7, rounded up to 3,409 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.147540983606557                          # control proportion
p1 <- 0.172413793103448                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1522443)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 3,409 (80% power), 4,563 (90% power)
 75% of observed effect: n per arm = 5,965 (80% power), 7,985 (90% power)
 50% of observed effect: n per arm = 13,206 (80% power), 17,678 (90% power)
power.prop.test: 3408.7 
Simulated power at n = 3,409 per arm: 0.799 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry-reported primary analysis is a Cochran-Mantel-Haenszel comparison with p = 0.773. The recalculated unadjusted comparison from the posted summary statistics gives p = 0.711. The recalculation is not a correction to the registry result: it uses a simpler, unadjusted method, whereas the registry identifies a stratified comparison. The registry record does not report the strata or enough methodological detail to reproduce that analysis from the posted summary alone.

The posted primary responder percentages are 15.0% for cabozantinib and 17.0% for mitoxantrone plus prednisone. The unadjusted recalculation gives a direct risk-difference estimate, but it should be interpreted as descriptive support for the simple comparison, not as the registry’s adjusted estimate. The two p-values are close in broad interpretation: neither indicates a statistically significant difference in the primary comparison.

The registry-reported method and result are the appropriate reference for the sponsor’s stated primary analysis. No discrepancy is flagged between the posted analysis and the recalculation. The registry record does not provide a fuller statistical analysis plan or details about the adjustment structure, so no stronger claim about the relationship between the methods is warranted.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is explicitly identified as the primary analysis, and bone scan response and overall survival are listed as secondary outcomes. The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a strategy for controlling the overall type I error across outcomes. Without those details, the interpretation of secondary p-values should remain cautious, particularly when more than one outcome is examined.

The primary analysis population is reported as the Intent to Treat population of 119 participants, comprising 61 in the cabozantinib arm and 58 in the mitoxantrone plus prednisone arm. The registry does not report how missing pain assessments, incomplete follow-up, or other missing outcome data were handled. It also does not report imputation procedures, sensitivity analyses for missingness, or reasons for missing data. The stated endpoint is based on participant self-reports, but the record does not specify how incomplete 7-day reporting periods were treated.

For the secondary outcomes, analysis populations and missing-data procedures are not reported in the registry record. The overall survival timeframe is stated as randomization until 78 deaths, but the record does not provide further details about censoring or the handling of participants without an observed death by the analysis cutoff. These details matter for interpreting time-to-event estimates and their uncertainty.

The record identifies randomization and quadruple masking, but it does not provide a complete statistical analysis plan. The original sample-size assumptions, interim-analysis plans, and any prespecified subgroup analyses are not reported in the registry record. Their absence from the record does not establish that such procedures were or were not used; it limits what can be assessed from the posted information.

16. 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: febrile neutropenia (7.0%), neutropenia (5.3%), abdominal pain (3.5%), pulmonary embolism (3.5%), nausea (3.3%).

For serious adverse events, the registry lists 16 affected participants among 60 at risk in the cabozantinib group and 15 among 57 at risk in the mitoxantrone plus prednisone group. For other adverse events, it lists 60 affected among 60 at risk and 57 affected among 57 at risk, respectively. These are posted counts and denominators; they should be read as registry summaries rather than as a complete account of each event’s timing, severity, or relationship to treatment.

The registry lists febrile neutropenia at 7.0%, neutropenia at 5.3%, abdominal pain at 3.5%, pulmonary embolism at 3.5%, nausea at 3.3%, and pneumonia at 3.3% among its top serious adverse event terms. The record does not specify an arm for each listed term in this summary, so these percentages should not be assigned to a particular group.

Deaths are not reported in the safety summary. The registry record also does not provide additional context in these fields about event duration, recurrence, attribution, or exposure time. The counts alone do not establish comparative safety or explain why any event occurred.

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

The primary results describe the proportion of participants meeting a defined pain-response threshold in each randomized group at the reported assessment. The observed percentages were 15.0% with cabozantinib and 17.0% with mitoxantrone plus prednisone. The registry-reported comparison did not show a statistically significant difference. The confidence intervals indicate that the estimates are imprecise, so the results should not be interpreted as demonstrating that the groups are identical.

A nonsignificant result is not proof of no effect, and it does not demonstrate equivalence. Establishing equivalence or noninferiority requires a prespecified framework and an appropriate margin; such a framework is not reported in the registry record. The posted results also do not establish that either treatment does or does not work. They describe this trial’s measured outcomes and the uncertainty around them.

The definition of pain response combines a participant-reported change with restrictions on opioid use. Thus, the endpoint reflects both reported pain intensity and the specified medication-use conditions. It does not summarize every aspect of pain experience, quality of life, or disease status. Bone scan response and overall survival address other outcomes and cannot be treated as interchangeable with pain response.

The trial enrolled 119 participants, and the primary analysis used the Intent to Treat population. The limited sample size and wide primary confidence intervals constrain the precision of the comparison. Missing-data procedures, detailed analysis assumptions, and the reason for termination are not reported in the registry record, leaving additional uncertainties that cannot be resolved from the posted information.

The soundest interpretation is therefore bounded: the registry reports similar primary responder percentages, a nonsignificant primary comparison, and uncertainty that remains substantial. Broader claims about clinical benefit, equivalence, or the reasons behind the observed outcomes go beyond what these results establish.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition, comparison method, and precision rather than through a single p-value. The primary endpoint is not simply a change in pain score: it requires a specified improvement in worst pain and no specified increase or addition in opioid use. That combined definition shapes what the responder percentages mean.

It also illustrates the distinction between an arm-specific estimate and a treatment contrast. The posted confidence intervals describe uncertainty in each group’s response percentage, while a direct comparison requires an estimate and uncertainty for the difference between groups. The registry-reported primary test does not post a corresponding effect estimate or confidence interval, and the simple recalculation uses a different method.

The record further shows that a nonsignificant primary result can coexist with a statistically significant secondary result. These outcomes address different questions, and multiplicity matters when several outcomes are assessed. Without a reported testing hierarchy or adjustment, secondary findings deserve more cautious interpretation.

Finally, sample-size illustrations based on observed effects are not the same as the original design justification or observed power. The original planning assumptions are not reported. Keeping these distinctions clear helps readers avoid turning a limited registry summary into stronger conclusions than its estimates, methods, and documentation support.

19. Limitations

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

Several trial-specific limitations affect interpretation. The primary response estimate is based on 119 participants, split between arms of 61 and 58, and the arm-specific confidence intervals are broad. This limits precision for the primary comparison. The registry-reported primary analysis gives a p-value but does not post an effect estimate or confidence interval for that adjusted comparison.

The record identifies a Cochran-Mantel-Haenszel method but does not report the strata or enough detail to reproduce the sponsor’s analysis. The simple recalculation is unadjusted and therefore does not resolve that reporting gap. The registry also does not report missing-data methods for participant-reported pain assessments, analysis populations for secondary outcomes, or sensitivity analyses.

The registry does not report a multiplicity strategy for the secondary outcomes, the trial’s original sample-size justification, an interim-analysis plan, or the reason the study was terminated. The status does not explain whether termination affected follow-up or the analyses. Further, the serious adverse event summary does not assign the listed serious event terms to specific arms, and deaths are not reported in that safety summary.

These are limitations of the information available in the registry record; they do not establish that procedures were absent from trial conduct or other documents. They do, however, restrict how fully the analysis, missingness, safety findings, and reasons for the final record status can be evaluated.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Cabozantinib (XL184) Versus Mitoxantrone Plus Prednisone in Men With Previously Treated Symptomatic Castration-resistant Prostate Cancer — NCT01522443.
• Registry record last updated 2018-05-23; status last verified 2018-04.
• Results first posted 2018-05-23.
• 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.

23. Record Summary

NCT01522443 is a randomized, quadruple-masked, phase 3, parallel-group trial of cabozantinib versus mitoxantrone plus prednisone in men with previously treated symptomatic castration-resistant prostate cancer. Enrollment was 119, and the primary endpoint was pain response at Week 6 confirmed at Week 12, reported at Week 12.

The registry reports responder percentages of 15.0% and 17.0% and a Cochran-Mantel-Haenszel p-value of 0.773. The primary comparison is not statistically significant, and the arm-specific intervals indicate limited precision. Bone scan response and overall survival were listed as secondary outcomes. The registry status is terminated; the reason is not reported in the registry record.