An Investigational Immuno-therapy Study of Nivolumab Compared to Sorafenib as a First Treatment in Patients With Advanced Hepatocellular Carcinoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Investigational Immuno-therapy Study of Nivolumab Compared to Sorafenib as a First Treatment in Patients With Advanced Hepatocellular Carcinoma (NCT02576509), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

This is a comparative question about outcomes under randomized assignment, not a direct statement about what will happen to an individual participant. Randomization is intended to support a fair comparison between assigned groups, but the registry record does not report details of how the randomization sequence was generated or concealed. Nor does it report the original statistical plan, the protocol's sample-size justification, or the intended decision threshold for the primary analysis. Those details matter when judging how the sponsor planned to interpret the result. The posted primary comparison should therefore be read in light of the estimates and uncertainty that are recorded, without inferring unreported design choices.

3. Trial Design

The registry identifies NCT02576509 as a randomized, multicenter Phase III study of nivolumab versus sorafenib for first-line treatment of advanced hepatocellular carcinoma. Its design is parallel-group, with no masking listed. The record names Bristol-Myers Squibb as sponsor and lists the study as completed. The study start date is 2015-12-07, and the primary completion date is 2019-05-30.

Enrollment is reported as 743. The primary endpoint population is all randomized participants. For the posted overall survival estimates, the Nivolumab 240 mg group has 371 participants and the Sorafenib 400 mg group has 372. These are the groups used in the reported primary comparison. The arm descriptions give the treatments and doses, but refer to specified dosing days without providing the full schedules in the registry record.

The primary outcome is overall survival, measured from randomization to death from any cause. The record states that participants still alive are censored at their last known alive dates and that the median estimates use Kaplan-Meier estimates. The primary comparison is reported as a hazard ratio using a Log Rank method. Secondary outcomes listed include objective response rate per BICR RECIST 1.1, progression-free survival, and outcomes by PD-L1 expression for overall survival, progression-free survival, and response. The registry lists five outcome measures and twelve analyses, but it does not provide a complete account of the analysis plan or the results for every listed analysis.

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.

Pre-Treatment Period

Reasons for not completing this period:

Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: all randomized participants

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over time from the date of randomization to the date of death due to any cause, assessed up to June 2019 (approximately 41 months).

Overall survival measures the time from randomization until death from any cause. It is a time-to-event endpoint: the event is death, and the measured time is the interval from the specified starting point to that event. The registry defines the endpoint for all randomized participants and states that participants who are alive are censored at their last known alive dates. Censoring means that a participant contributes follow-up information up to the last time known to be alive, without being counted as having died at that point.

Overall survival is used because it captures time to death from any cause rather than relying on a particular tumor measurement or a judgment about why a participant died. Its definition does not require classifying the cause of death. The registry reports the median overall survival estimated with the Kaplan-Meier method, along with a 95% confidence interval for each group. A median is the estimated time by which half of the survival distribution has experienced the event; it is not the mean survival time and does not describe each participant's experience.

The comparison between groups is expressed as a hazard ratio. This summarizes the relative event rate over follow-up under the analysis, rather than subtracting the two group medians. A hazard ratio does not itself show the absolute survival probability at a particular time. The registry record does not report further details about the timing or completeness of follow-up beyond the stated assessment period, nor does it give the sponsor's full analytic plan for this endpoint.

7. Results Posted in the Registry

• Nivolumab 240 mg vs Sorafenib 400 mg: hazard ratio 0.85 (95% CI 0.71–1.02), reported p = 0.075 (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.

Objective Response Rate (ORR) Per BICR RECIST 1.1

• 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:
  • Sorafenib 400 mg: 7.0% (26/372) versus 15.4% (57/371) on control; risk difference -8.4 percentage points (95% CI -12.9 to -3.9), risk ratio 0.45 (0.29–0.71); 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 Sorafenib 400 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Progression-Free Survival (PFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Nivolumab 240 mg vs Sorafenib 400 mg: hazard ratio 0.93 (95% CI 0.79–1.10) (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 Nivolumab 240 mg vs Sorafenib 400 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add information about tumor response, progression, and outcomes by PD-L1 expression. The posted response estimates and comparison indicate a different response pattern between the groups, while the progression-free survival estimates and hazard ratio are closer in their direction and less conclusive in their uncertainty. These endpoints do not establish the primary overall survival result; they describe distinct outcomes with their own definitions and analyses.

The overall pattern should be read alongside the primary result rather than as a collection of independent confirmations. Response is a measure of objective tumor change under the named criteria, whereas progression-free survival combines progression and death over time. Neither is identical to overall survival. A secondary outcome may support biological or clinical context, but agreement or disagreement with the primary endpoint does not by itself determine the validity of either result.

The registry lists efficacy analyses by PD-L1 expression for overall survival and progression-free survival, as well as response by PD-L1 expression. Results for those analyses are not reported in the registry record. The result record also lists secondary outcomes beyond the estimates, so the absence of posted estimates limits assessment of the complete secondary-outcome pattern.

Unadjusted secondary findings generally carry less confirmatory weight when many outcomes or subgroup comparisons are examined. The more comparisons made, the more opportunity there is for apparently noteworthy findings to arise by chance. A multiplicity adjustment or a prespecified hierarchy can address this concern, but the registry record does not report whether either was used. The unadjusted response recalculation should therefore be interpreted as exploratory statistical context, not as an independently definitive claim. The same caution applies to secondary comparisons whose analysis plan and multiplicity handling are not stated.

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

• Objective Response Rate (ORR) Per BICR RECIST 1.1
• Progression-Free Survival (PFS)
• Efficacy Based on PD-L1 Expression - OS and PFS
• Efficacy Based on PD-L1 Expression - ORR

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help interpret the posted results. The record identifies time-to-event outcomes, group medians, confidence intervals, hazard ratios, and a Log Rank method for the primary comparison. These methods answer related but different questions, so their estimates should not be treated as interchangeable.

What does the Kaplan-Meier median describe?

As a general statistical explanation, the Kaplan-Meier method estimates the probability of remaining free of the event over follow-up while accounting for censoring. Participants who have not experienced the event contribute information until their last known follow-up. The estimated median is the point in time at which the estimated event-free proportion reaches its midpoint. It is a summary of the estimated distribution, not an arithmetic average of observed times and not a guarantee about an individual participant.

For overall survival, the event is death from any cause. For progression-free survival, the registry defines the event as the first objectively documented tumor progression or death. These definitions make clear that overall survival and progression-free survival capture different outcomes. The posted median for each endpoint should be understood in relation to its own event definition and follow-up information.

What does a hazard ratio express?

As a general explanation, a hazard ratio compares the instantaneous event rates between groups over follow-up. A value below the no-difference value favors the group in the numerator in the direction of a lower event hazard; a value above it points in the opposite direction. This interpretation concerns relative event rates and does not directly provide an absolute risk difference, a median difference, or the chance that a participant will experience an event.

The primary hazard ratio is reported as 0.85, with a 95% confidence interval from 0.71 to 1.02. The registry states that the comparison uses a Log Rank method. The reported p-value is 0.075. A p-value is a measure of how unusual the observed result, or a more extreme result, would be under a specified null model and test assumptions. It is not a measure of effect size, nor is it the probability that the result occurred by chance. The registry record does not provide the full statistical plan, so details such as any covariate adjustment, handling of departures from model assumptions, or interim testing are not reported in the registry record.

Why do confidence intervals matter?

As a general explanation, a confidence interval communicates sampling uncertainty around an estimate. A narrower interval indicates greater precision, while a wider interval leaves a broader set of plausible values. The confidence intervals in the registry are reported at the 95% level. They should be read together with the point estimate, since a point estimate alone hides uncertainty. An interval that spans the no-difference value is compatible with effects in more than one direction under the interval's construction; that does not prove the absence of an effect.

How are response and progression outcomes different?

Objective response rate is a binary outcome expressed as the percentage of participants classified as having an objective response under the named assessment criteria. The registry specifies BICR RECIST 1.1. The listed response estimates are 15.4% for nivolumab and 7.0% for sorafenib, each with a 95% confidence interval. The registry also reports a difference of ORRs of 8.3 with a 95% confidence interval from 3.9 to 12.7, and an odds ratio of 2.41 with a 95% confidence interval from 1.48 to 3.92. These summaries describe response, not survival duration.

Progression-free survival is a time-to-event outcome, with progression or death counted as the event. Its posted medians are 3.68 months for nivolumab and 3.75 months for sorafenib. The reported hazard ratio is 0.93, with a 95% confidence interval from 0.79 to 1.10. The registry does not report a p-value for this comparison. The response and progression-free survival findings should be understood as secondary results and not as substitutes for the primary endpoint.

What does over-dispersion mean in general?

Over-dispersion is a general statistical issue that occurs when observed variability is greater than a model assumes. When it is present, standard errors can be too small if the model does not account for the extra variability, making intervals appear more precise than warranted. The registry record does not identify over-dispersion as an issue in this trial, and no conclusion about it can be drawn from the posted results.

11. Confidence Intervals and Precision

Precision is conveyed chiefly by the confidence intervals around the reported estimates. For overall survival, the median estimate for Nivolumab 240 mg is 16.39 months, with a 95% confidence interval from 13.93 to 18.37 months. For Sorafenib 400 mg, the median estimate is 14.69 months, with a 95% confidence interval from 11.89 to 17.22 months. These ranges describe uncertainty in the estimated medians, not the spread of individual survival times.

The primary hazard ratio is 0.85, and its 95% confidence interval runs from 0.71 to 1.02. Because that interval includes values on both sides of the no-difference value, the point estimate alone gives a more definite impression than the uncertainty supports. The interval allows a range of comparative effects, including values that do not favor nivolumab. The p-value of 0.075 is another summary of uncertainty under the reported test, but it does not replace the confidence interval or establish the probability that a treatment effect exists.

Secondary estimates also have uncertainty. The objective response estimates have confidence intervals, as do the reported difference of ORRs and odds ratio. The PFS medians and hazard ratio are likewise reported with confidence intervals. Precision varies by estimate, and the interval should be considered with the outcome definition and analysis population. No results for the listed PD-L1 subgroup analyses are reported in the registry record, so their precision cannot be assessed.

In general, confidence intervals quantify uncertainty under the method used; they do not account automatically for every possible bias, missing-data issue, or unreported analysis choice. The record does not provide enough information to evaluate all such factors. A narrow interval would not by itself resolve limitations in study conduct, while a broad interval signals that the estimate remains uncertain even if the study was randomized.

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 effects, not the original trial design calculations. The registry record does not report the trial's own original sample-size assumptions or justification. For time-to-event outcomes, including overall survival and progression-free survival, the planning values are total event counts. For the binary response outcome, they are participants per arm.

The stated illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The rows for 100% of the observed effect represent planning around the full observed effect; the rows for 75% and 50% represent smaller target effects. For overall survival, the total events listed for 80% power are 1,189, 2,114, and 4,755 across those effect assumptions, respectively. For 90% power, the corresponding event totals are 1,592, 2,829, and 6,366.

For objective response, the figures are participants per arm. Planning for 100% of the observed effect gives 222 participants per arm for 80% power and 296 for 90% power. Planning for 75% of the observed effect gives 426 participants per arm for 80% power and 570 for 90% power. Planning for 50% of the observed effect gives 1,030 participants per arm for 80% power and 1,378 for 90% power. The same general relationship applies to event-based planning: smaller effects require more information, which means more participants or more events.

In plain terms, the 80% and 90% power targets describe the chance of detecting the assumed effect under the stated planning model if that effect were present. Higher target power generally requires more information. These figures are planning illustrations, not observed power.

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 = 0.850, so ln(HR) = -0.1625.
2. d = 4 × (1.96 + 0.842)² / [ln(0.850)]² = 1,188.7, rounded up to 1,189 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 <- 0.85                              # 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(2576509)
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 = 1,189 (80% power), 1,592 (90% power)
 75% of observed effect: events = 2,114 (80% power), 2,829 (90% power)
 50% of observed effect: events = 4,755 (80% power), 6,366 (90% power)
Simulated power with 1,189 events: 0.794 (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 2,158 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 743 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 <- 14.69          # control-arm median, months (converted from the posted unit)
hr          <- 0.85          # 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: 1744         p (1-sided)   0.0001
  Events: 537        ~HR at bound   0.7258
    Month: 19    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.85   0.0338
    IA 2: 67%                   Z   2.5114
      N: 2158         p (1-sided)   0.0060
 Events: 1073        ~HR at bound   0.8578
    Month: 31    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.85   0.5603
        Final                   Z   1.9930
      N: 2158         p (1-sided)   0.0231
 Events: 1609        ~HR at bound   0.9054
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.85   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 comparison is reported by the sponsor as a hazard ratio of 0.85, with a 95% confidence interval from 0.71 to 1.02 and a Log Rank p-value of 0.075. For this time-to-event endpoint, the statistical summary uses the sponsor-reported hazard ratio; the posted median estimates remain useful descriptions of each group but do not reproduce the hazard-ratio analysis.

For objective response, the sponsor reports a difference of ORRs of 8.3, with a 95% confidence interval from 3.9 to 12.7, and an odds ratio of 2.41, with a 95% confidence interval from 1.48 to 3.92. A simple unadjusted recalculation from the posted summary statistics gives a p-value of <0.001 for the response comparison. That recalculation is not a substitute for the sponsor's analysis: it may not reflect the sponsor's analysis population, covariate handling, or other choices that are not described in the registry record. No discrepancy is flagged between the posted sponsor results and the available comparison details.

Recalculated results are useful as a check on the arithmetic implied by posted summaries, but they cannot recover details of an analysis that are not reported. When a sponsor result is available, it remains the primary reported analysis to interpret. The registry record does not give a comparable sponsor p-value for progression-free survival.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when a study examines more than one endpoint, analysis, subgroup, or comparison. Each test can produce an apparently notable result by chance, and the chance of at least one such finding can increase as more tests are considered. This is why confirmatory trial plans often specify a primary endpoint, define how secondary tests will be interpreted, and describe any adjustment or testing hierarchy.

The registry identifies overall survival as the primary endpoint and lists several secondary outcomes, including response, progression-free survival, and analyses by PD-L1 expression. It reports twelve analyses. However, multiplicity procedures, any prespecified testing order, and the intended confirmatory status of individual secondary analyses are not reported in the registry record. Without that information, secondary p-values or confidence intervals should not be treated as though they necessarily control the overall chance of false-positive findings.

Missing-data and analysis-population details are also incomplete. For overall survival, the record states that living participants are censored at the last known alive dates and defines the population as all randomized participants. This does not describe every aspect of follow-up, such as the amount of missing status information, or how other potential data issues were handled. For the response and progression-free survival results, the record gives group counts and outcome definitions but does not provide a complete account of the analysis populations, missing observations, or sensitivity analyses.

The registry also does not report interim analyses, stopping rules, the original sample-size justification, or the full statistical analysis plan. Those omissions do not invalidate the posted results, but they limit evaluation of whether analyses and decisions followed prespecified procedures. The reported estimates can be interpreted descriptively, while stronger claims about confirmatory testing require information not reported in the registry record.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: malignant neoplasm progression (19.3%), general physical health deterioration (3.9%), abdominal pain (3.0%), hepatic failure (2.7%), ascites (2.5%).

The registry reports serious adverse event figures by treatment group. For Nivolumab 240 mg, 216 participants are listed as affected among 367 at risk; for Sorafenib 400 mg, 216 are listed as affected among 363 at risk. These are counts, not comparative risk estimates. The record also gives other adverse event figures: 339 affected among 367 at risk for nivolumab and 351 among 363 at risk for sorafenib. The registry record does not define further how these two categories relate to one another.

Deaths are listed as 321 for nivolumab and 335 for sorafenib. The adverse-event figures alone do not establish that an event was caused by treatment, and the death counts do not identify cause. The most frequently listed serious terms include malignant neoplasm progression at 19.3%, general physical health deterioration at 3.9%, abdominal pain at 3.0%, hepatic failure at 2.7%, ascites at 2.5%, and oesophageal varices haemorrhage at 2.2%.

These summaries are useful for describing what the record reports, but they are not a complete assessment of comparative safety. The registry record does not provide additional details about event timing, severity grading, exposure duration, or how events were attributed. Counts and percentages should therefore be read as registry safety summaries, not as proof that a treatment caused or prevented an event.

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

The posted results describe a randomized comparison of nivolumab and sorafenib for advanced hepatocellular carcinoma. The primary overall survival estimate is a hazard ratio of 0.85, with a 95% confidence interval from 0.71 to 1.02 and a p-value of 0.075. The interval leaves meaningful uncertainty around the estimate, including values compatible with effects in either direction. The result is not a precise estimate of a single underlying treatment effect.

The group medians provide an additional descriptive summary but do not replace the time-to-event comparison. They do not show survival probabilities at particular times, nor do they explain how the estimated survival distributions developed throughout follow-up. The registry record does not report the full statistical analysis plan, so it is not possible to reconstruct every planned inference or confirmatory decision rule from the posted results alone.

Secondary outcomes address response and progression as well as the listed PD-L1 analyses. The response findings have their own uncertainty and the progression-free survival result is not identical to the primary endpoint. Secondary outcomes can help characterize the pattern of evidence, but they should not be used to overrule the primary endpoint without considering prespecification, multiplicity, and analysis details. The PD-L1 subgroup results are not reported in the registry record.

These statistics do not establish what will happen to an individual participant, do not prove a treatment effect in either direction, and do not by themselves settle clinical decisions. They describe estimates for the trial groups under the recorded outcome definitions and analysis. Important details such as eligibility criteria beyond the broad population, the complete dosing schedules, missing-data handling, and the original statistical plan are not reported in the registry record. The appropriate reading is therefore measured: the posted estimates offer evidence about comparative outcomes, but their uncertainty and reporting limitations remain relevant.

19. Why This Trial Matters Statistically

This study is statistically informative because it places a randomized comparison of two first-line treatment strategies in a time-to-event framework, with overall survival designated as the primary outcome. Randomization supports comparison between assigned groups, while the all-cause death endpoint avoids relying on a subjective assessment of cause. The Kaplan-Meier medians and reported hazard ratio summarize different aspects of the survival data and illustrate why multiple measures are often needed to describe a trial result.

The primary hazard-ratio interval is important because it shows that the point estimate should not be treated as a settled effect. The estimate points in one direction, but the confidence interval extends across the no-difference value. The p-value provides a complementary test summary but does not remove the uncertainty or define clinical importance. This is a useful example of why interpretation should combine effect estimates, uncertainty, outcome definitions, and the study's prespecified analysis plan.

The secondary response and progression outcomes show how distinct endpoints may offer different views of treatment outcomes. Their interpretation also illustrates the statistical challenge of multiple analyses: without a reported multiplicity plan, secondary findings warrant caution. The absence of posted PD-L1 results and details about the analysis plan further demonstrates how registry reporting completeness affects what can be concluded.

Finally, planning illustrations based on observed effects are not a substitute for the original design justification. They can show the relationship between effect size, power targets, and the information required under stated assumptions, but they cannot reveal the trial's own design rationale or amount to observed power. Keeping these distinctions clear helps readers separate the trial's reported evidence from statistical explanation and planning scenarios.

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 this record constrain interpretation. The registry reports a primary completion date of 2019-05-30 and describes overall survival assessment up to June 2019 (approximately 41 months), but does not provide detailed follow-up distributions or time-specific survival probabilities in the results used. The median and hazard-ratio summaries cannot show every feature of the survival experience.

The record lists no masking. It also does not report how allocation was generated or concealed, or provide full eligibility criteria and dosing schedules. The primary outcome is defined for all randomized participants, and the record specifies censoring of participants known to be alive at their last known alive dates, but detailed missing-data and sensitivity-analysis procedures are not reported. For the secondary outcomes, the complete analysis populations are not described in the registry record.

The registry lists analyses by PD-L1 expression but does not report their results. It also does not report the original sample-size justification, interim analyses, stopping rules, the full statistical analysis plan, or multiplicity procedures. These omissions limit assessment of prespecification and confirmatory status. The response recalculation is unadjusted and should not be confused with the sponsor's full analysis. The planning illustrations use observed effects and stated assumptions rather than the trial's original design inputs. Finally, safety counts do not provide the detail needed to infer treatment causation or to compare event risk after accounting for exposure and other factors.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: An Investigational Immuno-therapy Study of Nivolumab Compared to Sorafenib as a First Treatment in Patients With Advanced Hepatocellular Carcinoma — NCT02576509.
• Registry record last updated 2025-02-17; status last verified 2025-01.
• Results first posted 2020-06-26.
• 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

NCT02576509 is a completed randomized, multicenter Phase III parallel-group study comparing nivolumab with sorafenib as first-line treatment for advanced hepatocellular carcinoma. The registry lists no masking and records enrollment of 743. The primary endpoint is overall survival, defined as time from randomization to death from any cause, with Kaplan-Meier median estimates and a sponsor-reported hazard ratio.

The reported primary hazard ratio is 0.85, with a 95% confidence interval from 0.71 to 1.02 and a Log Rank p-value of 0.075. The interval reflects uncertainty around the comparative estimate. Secondary results include objective response rate and progression-free survival; the registry also lists PD-L1 subgroup analyses, whose results are not reported in the registry record. Multiplicity procedures, the full analysis plan, and the original sample-size justification are not reported. Interpretation should account for that uncertainty and incomplete reporting.