CANTATA: CB-839 With Cabozantinib vs. Cabozantinib With Placebo in Patients With Metastatic Renal Cell Carcinoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for CANTATA: CB-839 With Cabozantinib vs. Cabozantinib With Placebo in Patients With Metastatic Renal Cell Carcinoma (NCT03428217), a randomized phase 2 study. The primary outcome is Progression-Free Survival (PFS) as Assessed by the Independent Radiology Committee (IRC).

2. Clinical Question

The contrast isolates the addition of CB-839 within a regimen that included cabozantinib in both groups. Because the study was randomized and placebo-controlled, the treatment groups were compared under a common trial framework; however, the registry record does not report the procedures used to generate the allocation sequence or conceal assignments. It identifies the trial as quadruple-masked, but does not specify which participant, investigator, or assessment roles were masked.

The clinical question concerns time until progression or death, not a single measurement at a fixed visit. It therefore asks about the timing of an event during follow-up, while allowing participants without a recorded event at analysis to contribute information up to their last evaluable radiographic assessment as described in the endpoint definition. Overall survival and investigator-assessed progression-free survival were also listed as secondary outcomes. The record does not report additional eligibility details beyond the advanced or metastatic renal cell carcinoma description, and the primary endpoint specifically refers to clear-cell disease.

3. Trial Design

CANTATA was a randomized, double-blind, placebo-controlled, parallel-group phase 2 clinical trial. The registry lists an enrollment of 444. The posted primary endpoint analysis includes 223 participants in the placebo-plus-cabozantinib group and 221 in the CB-839-plus-cabozantinib group. Its endpoint population is described as the intent-to-treat set: all randomized participants analyzed according to their assigned group.

The control regimen was placebo twice daily plus cabozantinib 60 mg once daily. The experimental regimen was CB-839 800 mg twice daily plus cabozantinib 60 mg once daily. Both were administered orally on Days 1 through 28 of each 28-day cycle, until progression by RECIST v1.1 or unacceptable toxicity, whichever occurred first. The registry identifies quadruple masking but does not report the specific roles or procedures covered by that description.

The record gives a study start date of 2018-04-24, a primary completion date of 2020-08-31, and a completed status. The primary endpoint was progression-free survival assessed by an Independent Radiology Committee. The stated analysis timeframe extends up to the primary analysis data cut-off date of 31 Aug 2020; maximum follow-up for this endpoint was 22.14 months. The registry also lists overall survival and investigator-assessed progression-free survival as secondary outcomes.

Several elements needed to reconstruct the full design are not reported in the registry record. These include the original sample-size justification, the planned target effect, detailed randomization and masking procedures, the schedule of endpoint assessments, and whether interim analyses were planned or conducted. The registry states the treatment stopping criteria but does not establish how other aspects of treatment exposure or post-treatment follow-up were handled. The record contains results for the primary and secondary endpoints, but it does not explain the distinct analysis populations or analytical choices behind each of the multiple reported hazard-ratio results.

4. Participant Flow and Accounting

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

Before assignment: Eligible participants were randomized in a 1:1 ratio to either the Pbo-Cabo arm or the CB-Cabo arm. Randomization was stratified by prior treatment with PD-1/PD-L1 inhibitor therapy (yes vs. no) and the International Metastatic Renal Cell Carcinoma Database Consortium (IMDC) Prognostic Risk Group (favorable vs. intermediate vs. poor).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Analysis Set: All randomized participants, analyzed according to the treatment group to which they are randomized.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS) as Assessed by the Independent Radiology Committee (IRC), measured over Up to the primary analysis data cut-off date of 31 Aug 2020. Maximum duration of follow-up for PFS was 22.14 months..

The primary endpoint was progression-free survival, or PFS, as assessed by an Independent Radiology Committee. The registry defines PFS as time from randomization to disease progression assessed by the committee using RECIST v1.1, or death from any cause, whichever occurred first. For participants with neither progression nor death recorded by the analysis, the stated censoring rule uses the date of the last evaluable radiographic disease assessment.

RECIST v1.1 classifies tumor response using changes in target lesions. The registry description defines complete response as disappearance of all target lesions and partial response as at least a 30% decrease in their summed diameters relative to baseline. Progressive disease requires at least a 20% increase relative to the smallest sum on study and an absolute increase of at least 5 mm. Stable disease falls between the criteria for partial response and progressive disease. These definitions make the endpoint a time-to-event measure based on radiographic assessment, with death also counted as an event.

General statistical context: a time-to-event endpoint uses both whether an event occurred and the timing of that event. Participants who have not experienced the event by the analysis can still contribute follow-up information, with censoring marking the end of the observed period rather than asserting that an event never occurs. PFS is used in trials when progression is a clinically relevant event and waiting for death alone would not capture the outcome of interest. The registry record does not report the scheduled imaging intervals or further operational details of committee review.

7. Results Posted in the Registry

• Pbo-Cabo vs CB-Cabo: hazard ratio 0.94 (95% CI 0.74–1.21), reported p = 0.653 (as reported in the registry).
• Pbo-Cabo vs CB-Cabo: hazard ratio 0.97 (95% CI 0.76–1.24), reported p = 0.819 (as reported in the registry).
• Pbo-Cabo vs CB-Cabo: hazard ratio 0.97 (95% CI 0.76–1.25), reported p = 0.835 (as reported in the registry).
• Pbo-Cabo vs CB-Cabo: hazard ratio 0.99 (95% CI 0.78–1.27), reported p = 0.948 (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.

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:
  • Pbo-Cabo vs CB-Cabo: hazard ratio 1.15 (95% CI 0.83–1.60), reported p = 0.387 (as reported in the registry).
  • Pbo-Cabo vs CB-Cabo: hazard ratio 1.17 (95% CI 0.85–1.62), reported p = 0.337 (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 Pbo-Cabo vs CB-Cabo and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Pbo-Cabo vs CB-Cabo and the control. The interval gives the range of effects that remain compatible with the data.

PFS as Assessed by the Investigator

• 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:
  • Pbo-Cabo vs CB-Cabo: hazard ratio 1.00 (95% CI 0.79–1.25), reported p = 0.969 (as reported in the registry).
  • Pbo-Cabo vs CB-Cabo: hazard ratio 1.01 (95% CI 0.80–1.27), reported p = 0.923 (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 Pbo-Cabo vs CB-Cabo and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Pbo-Cabo vs CB-Cabo and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists overall survival and investigator-assessed PFS as secondary outcomes. Across these outcomes, the posted hazard-ratio estimates and confidence intervals do not present a clear, precise separation between the randomized groups: the intervals include the null reference, and the reported p-values are not small. The median estimates provide additional descriptive summaries, but they do not turn the secondary outcomes into independent confirmation of the primary result.

The general pattern is broadly consistent with the primary endpoint in the limited sense that the secondary analyses do not show a precise statistical contrast. They do not establish that the treatments have the same effects, nor do they overturn or strengthen the primary finding by themselves. Overall survival measures a different event from PFS, while investigator-assessed PFS uses a different assessment source from the committee-assessed primary endpoint. Those distinctions matter when interpreting consistency across outcomes.

Unadjusted secondary results carry less weight because multiple outcomes and analyses create more opportunities for apparently notable results to arise by chance. A prespecified multiplicity strategy can address that concern, but such a strategy is not reported in the registry record. The secondary results should therefore be treated as supportive descriptive evidence rather than decisive standalone claims. Their interpretation is further limited because the record does not state whether the secondary analyses were powered for specific effects or how the multiple reported analyses within some outcomes relate to one another.

General explanation: a nonsignificant secondary result is not proof that no difference exists. Confidence intervals and the analysis context are needed to judge how much uncertainty remains. In this trial, the secondary findings should be read alongside, but not substituted for, the primary IRC-assessed PFS result. No claims about clinical benefit or lack of benefit follow from the secondary results alone.

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

• Overall Survival (OS)
• PFS as Assessed by the Investigator

9. Statistical Interpretation

10. Statistical Methods Explained

General explanation: randomized allocation creates a basis for comparing assigned treatment groups, while analysis according to randomized group preserves the intent-to-treat comparison. CANTATA's primary endpoint population is explicitly described as all randomized participants, analyzed in the group to which they were randomized. This definition does not mean that every participant necessarily had a progression or death event; participants without an event by the analysis can contribute censored follow-up as specified in the endpoint definition.

What does the hazard ratio express?

A hazard ratio compares the event rates over follow-up between groups under a time-to-event analysis. It is a relative measure, not a difference between the reported median times, and it is not itself a percentage of participants who experienced an event. A value of 1 is the usual reference for equal hazards. Values on either side indicate differing relative event rates according to the comparison's numerator and denominator, but the registry does not provide enough model detail to expand on the exact coding conventions beyond naming Pbo-Cabo versus CB-Cabo. The reported primary hazard ratio is 0.94, with a 95% confidence interval of 0.74 to 1.21.

The registry names the Log Rank method for the reported hazard-ratio analyses. General explanation: the log-rank test compares event-time experience across groups while taking account of the timing of observed events and censoring. The reported p-value indicates how compatible the observed test result is with a null comparison under the test's assumptions; it is not the probability that the null hypothesis is true. The primary p-value is 0.653. The registry does not report additional details about the calculation of the hazard ratio, such as the model specification or any covariates used.

How should the median and confidence interval be read?

The median PFS is the estimated time at which the event-time distribution reaches its midpoint. It is a summary of the distribution, not a measure of the average follow-up time and not a direct estimate of the hazard ratio. A 95% confidence interval communicates uncertainty in an estimated quantity under the statistical procedure used: in repeated applications of the method under its assumptions, intervals constructed this way would cover the target parameter at the stated rate. It is not a range that contains 95% of individual participant outcomes. The registry reports a 95% confidence interval for each primary median and for the hazard ratios.

The confidence interval for a hazard ratio can be compared with 1 to assess whether the data are compatible with equal hazards at the interval's stated confidence level. The primary interval extends from 0.74 to 1.21 and therefore includes that reference value. This is not proof of no difference: the interval also includes values on both sides of the reference. A p-value and confidence interval are related ways of conveying evidence and uncertainty, although the p-value alone does not show the range of effects compatible with the data.

What does censoring contribute?

General explanation: censoring records that the event time is not observed during the participant's available follow-up. It does not mean that the participant is removed from all analysis or that the event is known never to occur. The registry's stated PFS rule censors a participant without progression or death at the date of the last evaluable radiographic disease assessment. Interpretation of a time-to-event analysis relies on the censoring process being handled appropriately; the record does not report detailed censoring diagnostics or additional missing-data procedures.

Independent radiology review is the stated basis for the primary PFS assessment. This differs from investigator assessment, which is listed separately as a secondary outcome. The registry does not describe the committee's review process, whether readings were performed independently of treatment knowledge, or how disagreements were resolved. Although the trial is described as quadruple-masked, those operational assessment details are not reported.

Why are there multiple reported analyses?

The registry lists four Log Rank hazard-ratio analyses for the primary comparison, each with a 95% confidence interval and p-value. It does not label the distinct analysis populations, time points, or analytical specifications that would explain why four results appear. The estimates are all close to 1 and each reported interval includes 1, but the entries should not be averaged or selectively chosen without a documented rationale. No adjustment for multiple testing is described in the registry record. The sponsor's reported analysis remains the central reference for interpretation; the recalculated result does not flag a discrepancy.

General explanation: a statistical method can summarize data, but the assumptions and analysis plan determine how the summary should be interpreted. Details such as prespecified hypotheses, covariate adjustment, stratification, handling of protocol deviations, and the treatment of missing assessments matter for reproducibility. Those details are not reported in the registry record. Accordingly, interpretation should stay with the endpoint definitions, populations, methods, estimates, intervals, and p-values that are actually stated rather than filling gaps with assumed trial procedures.

11. Confidence Intervals and Precision

The primary medians are accompanied by 95% confidence intervals: 9.33 months, with an interval from 7.64 to 11.01, for placebo plus cabozantinib; and 9.17 months, with an interval from 7.59 to 11.1, for CB-839 plus cabozantinib. Both intervals express uncertainty in the estimated median. They are not ranges for individual PFS times, and the endpoints of the intervals should not be read as the earliest or latest possible outcomes for participants.

For the primary hazard ratio, the estimate is 0.94 and the 95% confidence interval is 0.74 to 1.21. The interval spans the null reference of 1 and includes values on either side. This means the estimate is not precise enough to distinguish a clear relative hazard difference from equal hazards at the stated interval level. The reported p-value, 0.653, is consistent with that interpretation. The interval is more informative than a point estimate alone because it displays a range of values compatible with the analysis, subject to the method's assumptions.

General explanation: precision depends on the amount and timing of observed information, not simply on the total number enrolled. In time-to-event analyses, event timing, censoring, and follow-up contribute to the information available. The registry reports a maximum PFS follow-up duration of 22.14 months, but does not provide the event count or a detailed account of censoring in the primary results. The posted record therefore does not allow a complete assessment of how each source of information contributed to the interval width.

The primary endpoint's four reported hazard-ratio intervals also include 1, and their p-values are not small. Because the registry does not explain the differences among those analyses, their precision should be interpreted individually as reported, without selecting one as the uniquely definitive analysis beyond the designated primary endpoint. The record does not provide a prespecified clinically important difference or equivalence margin. Thus, the intervals cannot be used to conclude that effects inside or outside a particular clinical threshold are unimportant.

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 event-count planning illustrations are total events, not participants per arm. This distinction applies to the time-to-event calculations for which the registry's illustration uses the Schoenfeld approach. The displayed values refer to hypothetical planning scenarios based on fractions of the observed effect; they are not the number of participants enrolled in CANTATA and should not be confused with the actual randomized group sizes.

The stated assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses an effect to detect equal to the stated fraction of the observed effect. The entries for 80% power and 90% power describe the total event counts that the illustration says would be needed to have those respective probabilities of detecting the assumed effect under the planning assumptions, if the assumptions and model apply. The 90% power column represents a higher target probability of detection than the 80% power column and therefore requires more event information in the displayed scenarios.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect show how the assumed target changes the planning requirement. A smaller effect is harder to distinguish from the null and requires more participants or, for these time-to-event calculations, more total events. The event-count figures are unusually large relative to the enrollment recorded for this trial; they are planning illustrations generated from the observed effect, not evidence that the trial was designed to accrue those event totals. The trial's original design assumptions and sample-size justification are not reported in the registry record.

These calculations are not observed power. Observed power is not a useful substitute for reading the confidence interval and p-value after results are known. The planning illustrations answer a hypothetical design question under specified assumptions; the actual trial results are interpreted using the posted estimates, intervals, and analysis methods.

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 = 0.940, so ln(HR) = -0.0619.
2. d = 4 × (1.96 + 0.842)² / [ln(0.940)]² = 8,200.3, rounded up to 8,201 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 <- 0.94                              # 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(3428217)
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 = 8,201 (80% power), 10,978 (90% power)
 75% of observed effect: events = 14,579 (80% power), 19,517 (90% power)
 50% of observed effect: events = 32,802 (80% power), 43,912 (90% power)
Simulated power with 8,201 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 12,902 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 444 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 <- 9.17          # control-arm median, months (converted from the posted unit)
hr          <- 0.94          # 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: 9082         p (1-sided)   0.0001
  Events: 3703        ~HR at bound   0.8852
     Month: 17    P(Cross) if HR=1   0.0001
               P(Cross) if HR=0.94   0.0338
     IA 2: 67%                   Z   2.5114
      N: 12902         p (1-sided)   0.0060
  Events: 7405        ~HR at bound   0.9433
     Month: 27    P(Cross) if HR=1   0.0060
               P(Cross) if HR=0.94   0.5603
         Final                   Z   1.9930
      N: 12902         p (1-sided)   0.0231
 Events: 11107        ~HR at bound   0.9629
     Month: 60    P(Cross) if HR=1   0.0250
               P(Cross) if HR=0.94   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 primary analysis reported in the registry is a Log Rank hazard-ratio analysis for Pbo-Cabo versus CB-Cabo, with an estimate of 0.94, a 95% confidence interval of 0.74 to 1.21, and p = 0.653. The registry also includes a recalculated analysis based on posted summary statistics. The record does not flag a discrepancy between the sponsor's own analysis and the recalculation, so the recalculation does not displace the sponsor's result.

In general, a recalculation from summary statistics is an unadjusted reconstruction and may not reproduce every detail of a trial's analysis plan or participant-level analysis. The sponsor's reported analysis takes precedence when a discrepancy is flagged; in this record, no such discrepancy is flagged. That does not resolve the registry's lack of detail about the specifications behind the four reported primary hazard-ratio analyses. Their separate purposes or populations are not explained, so the safest reading is to retain each as reported and avoid assuming that they represent distinct endpoints or independent evidence.

Both the reported estimate and its interval should be read together. The point estimate is close to 1, while the interval spans the reference value and supports uncertainty about the relative hazard. The p-value does not establish that the groups are equivalent, and the recalculation does not add an independent data source. It is another statistical representation of the posted summary information, not a new trial result.

16. Multiplicity, Missing Data and Analysis Populations

The registry record reports four primary PFS hazard-ratio analyses and multiple analyses for secondary outcomes, but does not explain the distinctions among the repeated analyses. It does not identify a multiplicity adjustment, a hierarchical testing sequence, or a prespecified strategy for controlling the chance of false-positive findings across endpoints and analyses. The absence of a reported adjustment does not prove that none was used in the full trial analysis; it means the registry record does not document one.

This matters because interpreting each p-value as if it were the sole planned test can overstate the strength of evidence when many outcomes or analyses are examined. The primary endpoint is identified in the record, which helps distinguish it from the secondary outcomes, but the status and purpose of each repeated hazard-ratio analysis are not described. Without those details, secondary findings and unexplained duplicate analyses should be viewed cautiously, and no isolated result should be elevated on the basis of its p-value alone.

The primary population is reported as intent-to-treat: all randomized participants analyzed according to their assigned group. This is an important analysis principle, but the registry does not report endpoint-specific numbers included in every analysis or explain missing data beyond the PFS censoring definition. For PFS, participants without progression or death at the analysis are censored at their last evaluable radiographic assessment. Further details about missing imaging, withdrawal, other censoring reasons, and sensitivity analyses are not reported in the registry record.

The registry also does not report whether interim analyses occurred, whether stopping boundaries were used, or how such analyses might relate to the reported p-values. The original sample-size justification and design assumptions are not reported either. These omissions limit the ability to assess whether the analyses followed a prespecified plan and how robust the conclusions are to alternative choices. They do not erase the posted results, but they narrow what can be concluded from the record alone.

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: pulmonary embolism (3.2%), diarrhoea (2.7%), pleural effusion (2.2%), acute kidney injury (1.8%), dyspnoea (1.8%).

The registry reports serious adverse events in 74 of 217 participants at risk in the placebo-plus-cabozantinib group and in 90 of 225 participants at risk in the CB-839-plus-cabozantinib group. Other adverse events were reported in 213 of 217 participants at risk and 222 of 225 participants at risk, respectively. Deaths are listed as 89 and 93 in the two groups. These are descriptive counts; the registry record does not provide a comparative statistical analysis of these safety figures in the posted summary.

The leading listed serious adverse event terms include pulmonary embolism at 3.2%, diarrhoea at 2.7%, pleural effusion at 2.2%, acute kidney injury at 1.8%, dyspnoea at 1.8%, and cholecystitis at 1.4%. These are term-specific reported percentages, not an exhaustive account of every event or a measure of treatment causality. The record does not provide the event-specific denominators or additional detail needed to reconstruct each percentage's calculation.

General explanation: raw adverse-event counts depend on the number at risk, time exposed, and how events are collected and classified. A difference in counts alone does not establish a causal difference between regimens. The registry record does not give exposure-adjusted rates, severity distributions beyond the serious-event listing, or detailed attribution information in these results. The safety figures should be read as the posted descriptive summary, not as a complete comparative safety assessment.

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

The posted primary results describe a comparison of CB-839 plus cabozantinib with placebo plus cabozantinib for IRC-assessed PFS in advanced or metastatic clear-cell renal cell carcinoma. The estimated medians are close, and the reported hazard ratio is near the null reference. Its 95% confidence interval includes 1, and the reported p-value is 0.653. Together, these figures do not provide a clear statistical separation between the groups in this analysis.

That finding is not the same as proof that the regimens are equivalent. To support equivalence or non-inferiority, a trial would ordinarily need a prespecified margin and a design and analysis addressing that question. Such a margin is not reported in the registry record. A confidence interval that crosses the null leaves uncertainty about the size and direction of the relative effect; it does not demonstrate that every clinically meaningful difference has been ruled out.

Nor does the result establish that either regimen is effective or ineffective in a broader clinical sense. The record describes a randomized trial comparison and reports time-to-event estimates, not a universal treatment conclusion. The sample is restricted to the trial population described, and the record does not provide enough eligibility or subgroup detail to support conclusions for other populations. No medical recommendation follows from these statistics.

The interpretation is also bounded by the information reported. The endpoint is defined, the intent-to-treat population is specified, and the registry gives a data cut-off and maximum follow-up. However, it does not report a full statistical analysis plan, the distinctions among repeated analyses, multiplicity handling, detailed censoring diagnostics, or interim-analysis procedures. These are relevant to judging confirmatory strength and reproducibility. The results can be read accurately as reported without assuming that unreported procedures were or were not performed.

Overall, the registry record presents uncertain evidence about the relative PFS hazard and does not establish a clear difference in the primary analysis. The secondary outcomes are also not a basis for a definitive treatment claim. A careful reading keeps the estimates, intervals, study population, and reporting limitations together rather than reducing the trial to a single p-value or median.

19. Why This Trial Matters Statistically

CANTATA illustrates why time-to-event results should be interpreted using more than a pair of median estimates. The primary endpoint reports median PFS in both groups, but the hazard ratio and its confidence interval address the relative event experience across follow-up. The interval around the reported hazard ratio includes the null reference, making uncertainty visible even though a point estimate is available. This is a central statistical lesson: a point estimate alone does not show how much the data constrain plausible effects.

The trial also shows the importance of matching a statistical summary to its design. PFS is defined from randomization to progression or death, with censoring at the last evaluable radiographic assessment when neither event has occurred. That definition makes follow-up and censoring part of the interpretation. The independent committee assessment is the primary endpoint source, while investigator-assessed PFS is a separate secondary measure. Treating these as interchangeable would obscure their distinct assessment bases.

The registry's multiple reported hazard-ratio results and the absence of detail about their differences provide a practical example of why analysis documentation matters. Without knowing which populations, specifications, or testing roles distinguish analyses, readers cannot reconstruct their relationship or infer a multiplicity strategy. Clear reporting of these choices is essential for understanding the evidential weight of each result.

Finally, the sample-size illustrations underscore the difference between a hypothetical planning calculation and the study's original design or observed result. The illustrations use stated assumptions and effect fractions, while the trial's original sample-size justification is not reported. Keeping those separate prevents planning scenarios from being mistaken for observed power or actual enrollment targets. Together, these features make the record useful for teaching disciplined interpretation of effect estimates, uncertainty, analysis populations, and reporting gaps.

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 limitations specific to interpretation of this trial follow from what the registry reports. The primary comparison includes medians and multiple hazard-ratio analyses, but the record does not explain why four primary hazard-ratio results are listed or what distinguishes them. Without that information, their roles cannot be reconstructed, and it is not possible to identify which analysis specifications, if any, were prespecified as sensitivity analyses.

The primary PFS analysis is based on independent radiology review, but the registry does not describe the review workflow, assessment schedule, handling of disagreements, or whether imaging review was independent of treatment knowledge in practice. The trial is listed as quadruple-masked, but the record does not identify the four roles covered by masking. These details would help readers understand how assessment and masking were implemented.

The registry defines censoring for participants without progression or death, but does not report the number censored, reasons for censoring, completeness of radiographic assessments, or sensitivity analyses addressing missing assessments. Maximum follow-up is reported, but the event count and follow-up distribution are not included in the posted primary summary. The available information therefore does not support a detailed evaluation of censoring patterns or endpoint ascertainment.

The original sample-size justification, target effect, and planned analysis assumptions are not reported in the registry record. Nor are interim-analysis procedures or multiplicity adjustments described. The existence of planning illustrations based on observed effects does not fill those gaps. Additional details about eligibility criteria and subgroup composition are also not included in the record presented, limiting assessments of generalizability beyond the stated advanced or metastatic clear-cell population.

Safety reporting is descriptive, with counts and a list of leading serious event terms; exposure-adjusted rates, event-specific analysis details, and a comparative statistical assessment are not reported. These limitations do not negate the posted outcomes, but they constrain the degree to which the trial can be independently reproduced or fully evaluated from the registry record alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: CANTATA: CB-839 With Cabozantinib vs. Cabozantinib With Placebo in Patients With Metastatic Renal Cell Carcinoma — NCT03428217.
• Registry record last updated 2023-03-20; status last verified 2023-02.
• Results first posted 2023-03-20.
• 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

CANTATA is a completed randomized, double-blind, placebo-controlled, parallel-group phase 2 trial of CB-839 plus cabozantinib versus placebo plus cabozantinib in advanced or metastatic renal cell carcinoma. The registry reports enrollment of 444 and defines the primary analysis population as all randomized participants analyzed according to assigned group.

The primary endpoint was progression-free survival assessed by an Independent Radiology Committee using RECIST v1.1. The reported medians were 9.33 months for placebo plus cabozantinib and 9.17 months for CB-839 plus cabozantinib. The reported hazard ratio was 0.94, with a 95% confidence interval of 0.74 to 1.21 and p = 0.653. The interval includes 1, so the primary estimate remains uncertain about the relative hazard.

Overall survival and investigator-assessed PFS were listed as secondary outcomes. The registry record does not report the original sample-size justification, a multiplicity strategy, interim-analysis details, or the distinctions among the multiple reported hazard-ratio analyses. The results are therefore best read with attention to their uncertainty and the limits of the available analysis documentation.