Nivolumab in Treating Patients With Localized Kidney Cancer Undergoing Nephrectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nivolumab in Treating Patients With Localized Kidney Cancer Undergoing Nephrectomy (NCT03055013), a randomized phase 3 study. The primary outcome is Recurrence-free Survival (RFS) Rate at 5 Years.

2. Clinical Question

3. Trial Design

PROSPER RCC is a phase 3 randomized, single-masked, parallel-group trial sponsored by the National Cancer Institute. The registry lists enrollment of 819 and a status of active, not recruiting. The study started on 2017-04-28, and its primary completion date is 2023-05-24. Which party was masked is not reported in the registry record.

The comparison is perioperative nivolumab plus nephrectomy against nephrectomy followed by observation. The intervention description includes nivolumab before and after surgery, while the comparator description specifies surgery followed by observation. Nephrectomy could be partial or radical in either arm. Further details of the post-operative nivolumab schedule beyond the listed cycles are not reported in the registry record.

The primary outcome is recurrence-free survival rate at 5 years. The registry states that it was assessed at 20 weeks, 40 weeks, then every 3 months for patients <2 years from randomization, then every 6 months for 3 years. The primary analysis includes all randomized RCC patients. The posted arm estimates use 381.0 participants in Arm A and 399.0 in Arm B.

The registry also lists recurrence-free survival at 3 years among patients with clear cell histology and overall survival at 5 years as secondary outcomes. Their analysis populations differ from the primary population as reflected in the posted arm counts. The allocation ratio, details of sequence generation and concealment, and the trial’s original sample-size assumptions 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: All randomized RCC patients were included in this analysis.

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.

Population: All randomized RCC patients are included in this analysis.

6. Primary Endpoint

The registry lists the primary outcome as Recurrence-free Survival (RFS) Rate at 5 Years, measured over Assessed at 20 weeks, 40 weeks, then every 3 months for patients <2 years from randomization, then every 6 months for 3 years.

The primary endpoint is recurrence-free survival (RFS) rate at 5 years. RFS measures the time from randomization until disease recurrence or death from any cause. The registry treats patients who did not undergo nephrectomy or were not disease-free following nephrectomy as having an event at day 1. Patients alive without an event are censored at their last disease evaluation.

This endpoint is useful because it incorporates both the timing of recurrence or death and the experience of participants who have not had an event by the end of their observed follow-up. A Kaplan-Meier estimate can use the available follow-up for those participants rather than treating everyone without a recorded event as though their future status were known. Censoring records the point at which event status is no longer observed; it does not establish that an event never occurred.

The five-year rate is therefore an estimated proportion recurrence-free and alive at that time, rather than a simple count of events divided by the number enrolled. Its interpretation depends on the event definition, follow-up, and censoring process. How censoring was handled beyond the stated endpoint definition, and whether additional sensitivity analyses were planned, are not reported in the registry record.

7. Results Posted in the Registry

• Arm B (Nephrectomy Only): 0.5% (2/399) versus 0.5% (2/381) on control; risk difference -0.0 percentage points (95% CI -1.0 to 1.0), risk ratio 0.95 (0.14–6.74); unadjusted two-proportion z-test p = 0.963.

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.

Recurrence-free Survival (RFS) Rate at 3 Years Among Patients With Clear Cell Histology

• 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:
  • Arm B (Nephrectomy Only): 0.6% (2/325) versus 0.7% (2/303) on control; risk difference -0.0 percentage points (95% CI -1.3 to 1.2), risk ratio 0.93 (0.13–6.58); unadjusted two-proportion z-test p = 0.944.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Nephrectomy Only) and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival Rate at 5 Years

• 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:
  • Arm B (Nephrectomy Only): 0.7% (3/415) versus 0.7% (3/404) on control; risk difference -0.0 percentage points (95% CI -1.2 to 1.1), risk ratio 0.97 (0.20–4.79); unadjusted two-proportion z-test p = 0.974.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Nephrectomy Only) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the clinical questions beyond the primary five-year RFS endpoint: one considers RFS at 3 years among patients with clear cell histology, and the other considers overall survival at 5 years. Their posted estimates and intervals indicate uncertainty in each comparison, and neither secondary endpoint has a sponsor-reported analysis listed in the registry record.

As a broad pattern, the secondary results do not supply a clear, separately reported inferential result that changes the interpretation of the primary analysis. They should be considered alongside, not instead of, the primary time-to-event result. The secondary measures also differ in endpoint, time point, or analysis population, so they do not constitute interchangeable replications of the primary finding.

Unadjusted secondary results generally carry less inferential weight when several outcomes are examined. Testing multiple outcomes increases the opportunity for apparently notable results to occur by chance. A multiplicity procedure can control that risk, but whether one was planned or used is not reported in the registry record. The number of posted secondary outcomes is 2, and the record lists 1 reported analysis overall. Without a reported multiplicity strategy, secondary comparisons are best treated as supportive or exploratory rather than as independent confirmatory evidence.

Differences in the populations represented by secondary outcomes also matter. The clear-cell RFS outcome is restricted to that histology, while the primary analysis includes all randomized RCC patients. The overall-survival endpoint measures a different event from RFS. Those distinctions limit direct comparison across outcomes and make the primary endpoint’s own definition and analysis central to interpretation.

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

• Recurrence-free Survival (RFS) Rate at 3 Years Among Patients With Clear Cell Histology
• Overall Survival Rate at 5 Years

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas are relevant to interpreting the endpoint and its reported comparison. General explanations below describe the methods; trial-specific statements are limited to what the registry record reports.

What does a Kaplan-Meier estimate represent?

In general, Kaplan-Meier estimation describes the probability of remaining free of an event over time. At each event time, the estimate uses participants still under observation and event-free immediately before that time. Participants whose follow-up ends without a known event are censored at their last observed time. Censoring lets the analysis retain their observed event-free follow-up without claiming their later outcome is known.

For this trial, the event is recurrence or death from any cause, with the stated day-1 event rule for patients who did not undergo nephrectomy or were not disease-free following nephrectomy. The posted five-year rates are based on Kaplan-Meier estimates. They should not be read as the percentage of every enrolled participant whose outcome is known at five years, because participants may have different follow-up durations.

What does the log-rank test assess?

In general, the log-rank test compares the event experience of groups over follow-up. It uses information about when events occur and the participants at risk at those times. It is not the same as comparing two endpoint percentages at a single time point, and it does not by itself describe the magnitude of an effect. The registry reports a log-rank analysis for the primary comparison, but details of the test’s implementation are not reported in the registry record.

How should the Cox result be read?

In general, a Cox proportional hazards model expresses the relative event hazard between groups over time. A hazard is the instantaneous event rate among participants who remain event-free and under observation. The proportional-hazards model assumes the relative hazard is constant over time. The registry identifies a Cox proportional hazard parameter and reports a hazard ratio of 0.95, with a 95% confidence interval from 0.74 to 1.22 and p = 0.34. Whether the proportional-hazards assumption was examined, and what diagnostic results were obtained, are not reported in the registry record.

A hazard ratio is not a ratio of five-year RFS proportions, nor does it directly state the difference in time lived without an event for an individual participant. It is a group-level relative measure under the model. The confidence interval expresses uncertainty in that estimated relative hazard, conditional on the analysis and model.

Why distinguish the recalculation from the reported analysis?

General statistical principle: a time-to-event endpoint contains event timing and censoring information. A simple unadjusted recalculation from posted summary statistics does not recreate those data. Here the recalculated risk difference and its p-value are separate from the registry’s log-rank and Cox result. They should not be used to replace the sponsor’s stated time-to-event analysis or to imply that the primary endpoint was analyzed as a plain binary outcome.

For the primary comparison, the recalculated risk difference is -< 0.001, with an interval from -0.010 to 0.010 and p = 0.963. This result is not numerically aligned with the difference between the posted Kaplan-Meier estimates because the calculations represent different summaries and use different information. It is important not to read the recalculated p-value as the p-value for the registry’s primary time-to-event test.

Why does over-dispersion matter in general?

General statistical explanation: over-dispersion occurs when variability in observed data is greater than a model assumes. If a model treats outcomes as less variable than they are, its standard errors can be too small and its confidence intervals too narrow. The registry does not report an over-dispersion assessment or a model requiring such an adjustment for the primary endpoint; this concept is relevant as a general reminder that uncertainty estimates depend on model assumptions.

The trial-specific endpoint definition, follow-up schedule, and censoring statement are reported, but full statistical methods are not. Details such as covariate adjustment, stratification, handling of protocol deviations, sensitivity analyses, and tests of model assumptions are not reported in the registry record. Their absence limits reconstruction of the analysis, but does not itself show that the reported analysis was invalid.

11. Confidence Intervals and Precision

The 95% confidence intervals describe uncertainty around the estimated five-year RFS rates. For Arm A, the estimate is 0.63 with an interval from 0.577 to 0.688. For Arm B, it is 0.605 with an interval from 0.545 to 0.671. The intervals overlap substantially. Overlap alone is not a formal test of the difference between groups, so the registry’s reported comparative analysis is the relevant test result.

The Cox hazard ratio is 0.95, with a 95% confidence interval from 0.74 to 1.22. The interval includes 1, indicating that the data are compatible with a range of relative hazards on either side of equality. The interval is more informative about precision than the p-value alone: it shows that the estimate does not pin down a narrow range of plausible relative effects.

In general, a confidence interval is a method for expressing sampling uncertainty under the assumptions of the analysis. It does not mean that there is a 95% probability the fixed true effect lies inside this particular calculated interval. Nor does it account automatically for unreported sources of uncertainty, such as bias, incomplete follow-up, model misspecification, or multiplicity.

The registry does not report confidence intervals for every comparison or the detailed procedures used to calculate them. The posted intervals should therefore be interpreted as conditional on the registry’s analysis methods, rather than as a complete account of all uncertainty.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. For these proportion-based endpoints, the entries are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own sample-size justification is not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect is real and the assumptions hold. The 90% power column expresses the corresponding planning target for a 90% chance. These are design probabilities for a hypothetical study, not probabilities that the treatment is effective.

Rows planning for 100%, 75%, or 50% of the observed effect ask what enrollment would be needed to detect effects of those relative sizes. Smaller effects generally require more participants to distinguish them from random variation. The very large values in the planning figures reflect the small observed effect used as the basis for these illustrations; they should not be treated as a recommendation or as a re-description of the trial’s enrollment.

These calculations are not observed power. Observed power calculated from an observed effect largely restates the information in the effect estimate and its uncertainty, rather than providing an independent assessment of whether the study was adequate. The planning figures are most useful as conditional illustrations of how assumed effect size and desired power affect hypothetical sample-size requirements.

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 = 0.005; treatment proportion p₁ = 0.005; average p̄ = 0.005.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1010 = 0.1980.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1010 = 0.0850.
4. n = (0.1980 + 0.0850)² / (-0.0002)² = 1,428,863.4, rounded up to 1,428,864 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 <- 0.005249343832021                          # control proportion
p1 <- 0.0050125313283208                          # 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(3055013)
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 = 1,428,864 (80% power), 1,912,843 (90% power)
 75% of observed effect: n per arm = 2,554,782 (80% power), 3,420,128 (90% power)
 50% of observed effect: n per arm = 5,781,061 (80% power), 7,739,200 (90% power)
power.prop.test: 1428863 
Simulated power at n = 1,428,864 per arm: 0.802 (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’s reported primary analysis is the log-rank comparison with a Cox proportional hazards parameter. It gives a hazard ratio of 0.95, a 95% confidence interval from 0.74 to 1.22, and p = 0.34. This is the trial’s reported time-to-event analysis and uses the endpoint’s event timing and follow-up structure as described in the registry.

The unadjusted recalculation gives a risk difference of -< 0.001, a 95% confidence interval from -0.010 to 0.010, and p = 0.963. It is calculated from posted summary statistics and is not equivalent to the reported log-rank/Cox analysis. In particular, the registry’s RFS endpoint is a time-to-event outcome, while a simple recalculation from summary counts cannot reproduce the original event-time and censoring information.

The two p-values therefore answer questions under different calculations and should not be compared as though they were competing versions of the same test. The reported analysis should be used to describe the registry’s primary time-to-event result; the recalculation is supplementary and limited by the summary information available. The registry does not report further detail that would permit independent reconstruction of the full sponsor analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and two secondary outcomes. It reports one analysis, for the primary RFS comparison. A multiplicity adjustment, hierarchical testing sequence, or other plan for controlling the chance of false-positive findings across outcomes is not reported in the registry record. Consequently, secondary results should not be treated as though they were protected by a stated family-wise error strategy.

The primary analysis population is described as all randomized RCC patients. The registry gives arm-specific analysis counts for the primary outcome, but does not explain the difference between those counts and the enrollment figure. It also does not report a detailed account of exclusions, protocol deviations, or the handling of participants without endpoint information. The registry’s population statement does not by itself establish how every participant was handled in every analysis.

The endpoint definition states that patients alive without an event are censored at the date of last disease evaluation. This is a standard way of representing incomplete event follow-up in time-to-event analysis, but censoring is not the same as resolving the participant’s later outcome. Additional details about missing assessments, loss to follow-up, censoring patterns, and sensitivity analyses are not reported in the registry record.

The trial’s original analysis plan, including any interim analyses, stopping rules, covariate adjustments, and prespecified subgroup procedures, is not reported in the registry record. These gaps limit assessment of how fully the posted results reflect the original statistical plan. They are uncertainties about the available record, not evidence that a particular unreported procedure was or was not performed.

16. 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: lipase increased (4.8%), alanine aminotransferase increased (2.8%), rash maculo-papular (2.5%), serum amylase increased (2.5%), hyperglycemia (2.5%).

The serious adverse event figures are reported for participants at risk in each arm. In Arm A, 113 of 357 participants at risk were reported as affected by serious adverse events; in Arm B, 46 of 377 were affected. The registry also lists other adverse events affecting 278 of 357 participants in Arm A and 114 of 377 in Arm B. Deaths are listed as 48 and 40, respectively.

These are descriptive registry counts, not an adjusted comparison of safety between randomized groups. The record does not provide enough detail to determine event timing, duration, severity grading, relationship to treatment, or whether multiple events could be reported for a participant. The listed serious terms include Lipase increased at 4.8%, Alanine aminotransferase increased at 2.8%, Rash maculo-papular at 2.5%, Serum amylase increased at 2.5%, Hyperglycemia at 2.5%, and Anemia at 2.4%. The denominators for those term percentages are not reported in the registry record.

Differences in these counts should not be interpreted as causal treatment effects without the relevant definitions and analysis context. The registry record’s adverse-event summary is descriptive and does not replace a complete safety evaluation.

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

The posted results describe a randomized comparison of perioperative nivolumab plus nephrectomy with nephrectomy followed by observation. For the primary endpoint, the registry reports Kaplan-Meier five-year RFS estimates and a log-rank/Cox comparison. The estimated hazard ratio is 0.95, with a 95% confidence interval from 0.74 to 1.22 and p = 0.34. The interval includes the null value and remains compatible with a range of effects.

This result does not establish that the groups are identical, and it does not establish that one approach is superior. A non-significant test is not proof of no difference. The confidence interval conveys uncertainty, while the point estimate alone should not be treated as a definitive description of the treatment effect.

The endpoint is a composite time-to-event measure: recurrence or death from any cause, with a day-1 event classification for patients who did not undergo nephrectomy or were not disease-free following nephrectomy. It is therefore not a measure of recurrence alone. The five-year estimate also depends on follow-up and censoring; it is not simply an observed fraction of the full enrollment group.

The secondary outcomes and adverse-event counts add context but do not resolve the uncertainty in the primary comparison. The registry does not report a multiplicity plan for secondary outcomes, and the secondary endpoints differ in population or definition. The adverse-event counts are descriptive and should not be read as adjusted causal comparisons.

These findings are a statistical description of the registry record, not medical advice and not a conclusion about what treatment an individual should receive. The record’s status is active, not recruiting, and its available summaries do not provide every detail needed to assess the design, conduct, or full analysis independently.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary outcome is time-to-event, yet the registry also contains proportion estimates and summary-based recalculations. Those quantities are not interchangeable. The Kaplan-Meier rate uses event timing and censoring, while a simple summary-based comparison cannot reproduce the full time-to-event analysis. Keeping the estimand and method aligned prevents a crude calculation from being mistaken for the primary test.

The reported hazard ratio and confidence interval also illustrate why an estimate should be read together with its precision. The point estimate is close to 1, but the interval spans values on both sides of 1. The p-value alone cannot establish equivalence or rule out a meaningful effect; the interval makes the uncertainty visible.

The endpoint’s event definition is consequential. RFS includes recurrence or death and assigns an event at day 1 to patients who did not undergo nephrectomy or were not disease-free following it. Readers need that definition to understand what the estimated rate represents and which clinical events contribute to it.

Finally, the record illustrates limits of registry summaries. The population statement and arm counts are available, but detailed analysis plans, multiplicity procedures, missing-data handling, and model diagnostics are not. Statistical interpretation therefore requires separating what the record directly reports from what cannot be evaluated from the posted information. The planning illustrations likewise show how assumptions about effect size and desired power shape hypothetical enrollment needs; they are not observed trial power or evidence about treatment efficacy.

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.

The registry record does not report the original sample-size justification or the design assumptions used when the trial was planned. The posted planning illustrations use the observed effect and stated hypothetical assumptions, so they cannot establish whether the original enrollment target was appropriate.

Some design details are unavailable, including the allocation ratio, randomization procedures, allocation concealment, and which party was masked. The registry identifies the study as randomized, single-masked, and parallel, but does not provide those further particulars in the available record.

The primary analysis includes all randomized RCC patients, but the record does not explain the relationship between the enrollment figure of 819 and the primary arm counts of 381.0 and 399.0. Detailed participant flow, reasons for exclusions or missing outcomes, and handling of protocol deviations are not reported. The endpoint definition specifies censoring at the last disease evaluation, but censoring patterns and missing-data sensitivity analyses are not reported.

The reported primary analysis is a log-rank test with a Cox proportional hazards parameter. Model diagnostics, proportional-hazards assessment, adjustment or stratification details, and sensitivity analyses are not reported. The registry also does not report a multiplicity strategy for the secondary outcomes. These limits prevent a complete independent assessment of analysis choices from the registry record alone.

The treatment description gives the listed nivolumab cycles but does not report further details beyond the truncated post-operative schedule. The registry’s safety summary likewise does not provide full event definitions, timing, treatment attribution, or denominators for the listed serious-event term percentages. These omissions limit detailed interpretation without determining what the complete trial documentation may contain.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Nivolumab in Treating Patients With Localized Kidney Cancer Undergoing Nephrectomy — NCT03055013.
• Registry record last updated 2026-08-28; status last verified 2026-07.
• Results first posted 2024-04-25.
• 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

PROSPER RCC (NCT03055013) is a phase 3 randomized, single-masked, parallel study comparing perioperative nivolumab plus nephrectomy with nephrectomy followed by observation in patients with renal cell carcinoma. The registry lists enrollment of 819 and status as active, not recruiting.

The primary endpoint is five-year recurrence-free survival, defined as time from randomization to recurrence or death from any cause, with specified early event rules. The reported log-rank/Cox analysis gives a hazard ratio of 0.95 (95% CI 0.74 to 1.22; p = 0.34). Kaplan-Meier estimates are 0.63 for Arm A and 0.605 for Arm B.

Two secondary outcomes are posted: three-year RFS among patients with clear cell histology and five-year overall survival. The registry reports no sponsor analysis for those secondary outcomes. Detailed original design assumptions, multiplicity procedures, and several analysis and missing-data details are not reported in the registry record.