Phase 3 Study of Sitravatinib Plus Nivolumab vs Docetaxel in Patients With Advanced Non-Squamous Non-Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Study of Sitravatinib Plus Nivolumab vs Docetaxel in Patients With Advanced Non-Squamous Non-Small Cell Lung Cancer (NCT03906071), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This was a randomized, phase 3, parallel-group study with no masking. The registry lists 577 participants as the enrollment and identifies two treatment groups: nivolumab plus sitravatinib and docetaxel. For the primary overall survival result, 284 participants were included in the combination group and 293 in the docetaxel group. The registry's primary outcome population is the Intent-to-Treat population, comprising all randomized participants.

The study addressed advanced non-squamous non-small cell lung cancer after disease progression on or after platinum-based chemotherapy and checkpoint inhibitor therapy. The combination group received intravenous nivolumab on one of the listed schedules and oral sitravatinib once daily. The comparator group received intravenous docetaxel every 3 weeks. The registry describes the study as terminated. The reason for termination is not reported in the registry record, so the status alone does not explain why the study ended.

The listed study start was 2019-07-15 and the primary completion date was 2023-03-20. Overall survival was followed from randomization to death from any cause, with follow-up described as up to approximately 44 months. The registry also lists 15 outcome measures and two analyses, with secondary outcomes including adverse events, response, clinical benefit and progression-free survival. The posted secondary results include several outcomes, but not all of the listed secondary outcomes have results described in the record summarized in this analysis.

The registry record does not report the original statistical design assumptions or the reason for choosing the enrollment target. It also does not report a planned interim-analysis schedule. These omissions matter when interpreting the study's operating plan: calculations based on the observed results are not evidence of the sample size or decision rules originally used by the investigators.

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: Intent-to-Treat population: 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 From randomization date to date of death due to any cause (Up to approximately 44 months).

Overall survival measures the time from randomization until death from any cause. Participants who were not recorded as dying on study were censored at the date of their last on-study follow-up at which they were known to be alive, including follow-up data. The registry reports Kaplan-Meier estimation for the arm-specific medians and the Brookmeyer and Crowley (1982) method for their confidence intervals.

Time-to-event outcomes use both the event and the timing of the event. They can retain information from participants with different lengths of follow-up, including participants whose event has not occurred by the end of observation. Censoring records that a participant was known to be alive up to a particular follow-up time without treating that participant as having died at that time. In general, valid interpretation depends on how follow-up and censoring are handled; details beyond the definition are not reported in the registry record.

Overall survival is a direct outcome with a clear event definition: death from any cause. It is distinct from response or disease-progression outcomes, which concern tumor assessments or progression and may use different assessment procedures. The registry's primary analysis reports median overall survival for each group and a hazard ratio for the comparison. The medians describe the estimated time by which half of the relevant survival distribution has experienced the event; the hazard ratio summarizes the relative event rate over follow-up under the time-to-event model or test used for the reported comparison. They answer related but not identical questions.

7. Results Posted in the Registry

• Nivolumab and Sitravatinib vs Docetaxel: hazard ratio 0.86 (95% CI 0.70–1.05), reported p = 0.144 (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 Central Radiographic Assessment

• 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:
  • Docetaxel: 17.2% (50/290) versus 16.0% (45/282) on control; risk difference 1.3 percentage points (95% CI -4.8 to 7.4), risk ratio 1.08 (0.75–1.56); unadjusted two-proportion z-test p = 0.680.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Benefit Rate Per Central Radiographic Assessment

• 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:
  • Docetaxel: 64.5% (187/290) versus 75.5% (213/282) on control; risk difference -11.0 percentage points (95% CI -18.5 to -3.6), risk ratio 0.85 (0.77–0.95); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Docetaxel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

1-Year Survival Rate

• 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:
  • Docetaxel: 44.7% (131/293) versus 50.7% (144/284) on control; risk difference -6.0 percentage points (95% CI -14.1 to 2.1), risk ratio 0.88 (0.74–1.05); unadjusted two-proportion z-test p = 0.150.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the description beyond overall survival. They include radiographic response and clinical benefit, survival at a fixed time point, progression-free survival, and safety outcomes. These measures address different aspects of the trial and are not interchangeable with the primary endpoint. The overall survival result remains the central time-to-event comparison specified as primary in the registry.

Across the posted binary outcomes, the arm-level estimates do not all point in the same descriptive direction. The recalculated unadjusted comparison for clinical benefit has a p-value of 0.004, while the unadjusted comparisons for objective response and one-year survival have p-values of 0.68 and 0.15. The pattern does not change the primary overall survival result, whose sponsor-reported p-value is 0.144 and whose confidence interval includes 1. Secondary outcomes can add context, but they cannot be used as substitutes for the primary endpoint.

In general, secondary outcomes are often numerous and may be correlated. Testing many outcomes without an adjustment or prespecified sequence increases the chance that at least one comparison will appear statistically notable by chance alone. The registry lists 15 outcome measures, but the record does not report a multiplicity strategy for the secondary results. Consequently, an isolated unadjusted secondary p-value should be interpreted cautiously and should not be treated as confirmatory evidence on its own.

The registry outcome list includes adverse events, central radiographic assessments and progression-free survival, but results are not described for every listed outcome in the posted results. Lack of a posted result should not be interpreted as a null finding. The reason that some listed outcomes do not have results in the record is not reported in the registry record.

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

• Number of Participants With Treatment-Emergent Adverse Event (TEAEs)
• Number of Participants With Treatment-Emergent Adverse Events (TEAE) Leading to Study Drug Discontinuation
• Number of Participants With Maximum Post Baseline Hematology Grade Results
• Number of Participants With Maximum Post Baseline Chemistry Grade Results
• Objective Response Rate (ORR) Per Central Radiographic Assessment
• Duration of Response (DOR) Per Central Radiographic Assessment
• Clinical Benefit Rate Per Central Radiographic Assessment
• Progression-Free Survival (PFS) Per Central Radiographic Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. The event is death from any cause, and the time origin is randomization. Participants without a recorded death were censored at their last on-study follow-up date when they were known to be alive. This approach allows the analysis to use follow-up from participants who have not had the event by the time their observation ends, rather than treating their follow-up as a death or discarding it.

The registry reports Kaplan-Meier estimation for overall survival. In general, the Kaplan-Meier method estimates the probability of remaining event-free over time while accounting for censored follow-up. It produces a survival curve, from which a median can be estimated as the time at which the estimated survival probability reaches 50%. The reported medians are 12.22 months for nivolumab and sitravatinib and 10.58 months for docetaxel. Their confidence intervals were calculated using the Brookmeyer and Crowley (1982) method, as stated in the registry.

The comparison between treatment groups is reported as a hazard ratio and a log-rank test. The hazard ratio is 0.86, with a 95% confidence interval from 0.70 to 1.05, and the reported p-value is 0.144. In general, a hazard ratio compares the event rates between groups over follow-up; a value of 1 corresponds to equal rates in the comparison, while values on either side indicate different relative rates under the analysis. The ratio is not a comparison of median survival times, and it should not be read as the percentage of participants who survived.

The log-rank test evaluates evidence for a difference between time-to-event patterns over observed follow-up. In general, the test uses event timing and the numbers at risk over time, rather than reducing the comparison to a single time point. Its p-value describes how compatible the observed data are with a null comparison under the test's assumptions. A p-value is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect.

What does the confidence interval describe?

In general, a confidence interval is a range of values produced by a method designed to have a stated long-run coverage rate under its assumptions. A 95% confidence interval communicates uncertainty in the estimate; it does not mean that there is a 95% probability that the particular interval contains the true value. For the hazard ratio, the reported interval extends from 0.70 to 1.05. Since the interval includes 1, the estimate is compatible with a range that includes no relative difference as well as values on either side.

The estimates for the secondary binary outcomes are percentages with 95% confidence intervals. Objective response was assessed per central radiographic assessment, as were clinical benefit and progression-free survival in the outcome list. Objective response and clinical benefit concern participant classifications over an assessment period, rather than time to death. The unadjusted recalculations compare posted group-level proportions; the registry does not list sponsor-reported analyses for the response and clinical-benefit outcomes described in the results. These calculations should therefore not be mistaken for sponsor analyses or for a complete prespecified analysis plan.

In general, binary outcomes are affected by both the number of participants and the number classified as having the outcome. A confidence interval for a percentage represents uncertainty in the estimated proportion. A comparison of two percentages can be expressed in different ways, including a difference in proportions or a ratio. Those measures have different reference values and interpretations. The arm-level percentages and their intervals are the clearest descriptive summaries; any inferential comparison also depends on its method and on how multiple outcomes are handled.

For secondary outcomes, the recalculated unadjusted p-values are 0.68 for objective response, 0.004 for clinical benefit, and 0.15 for one-year survival. In general, unadjusted p-values do not account for testing multiple outcomes. When many outcomes or comparisons are examined, the chance of at least one apparently notable result can increase. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary endpoints. This makes the secondary p-values less conclusive than a result from a fully described, prespecified testing strategy.

The reported primary comparison is the sponsor's hazard ratio and log-rank analysis. The recalculated summaries from posted arm-level data do not replace it. For time-to-event outcomes, the event times, censoring information and analysis details are needed to reproduce the comparison; arm-specific medians and their intervals alone are not enough to reconstruct the reported hazard ratio or log-rank test.

In general, over-dispersion occurs when observed variation exceeds what a statistical model assumes. It can make standard errors too small and confidence intervals too narrow if the model does not account for the extra variation. The registry record does not report an over-dispersion analysis, and over-dispersion is not a stated feature of the posted primary endpoint analysis. This general concept should not be taken as evidence that over-dispersion affected this trial.

Missing-data and analysis-population details are also part of statistical interpretation. For overall survival, the record defines censoring for participants not recorded as dying on study and specifies the Intent-to-Treat population. The record does not provide a detailed account of missing outcome data for each secondary endpoint, the handling of missing radiographic assessments, or sensitivity analyses. Without those details, the reported results can be described, but their robustness to alternative assumptions about missing observations cannot be assessed from the registry record.

11. Confidence Intervals and Precision

The arm-specific median overall survival estimates are 12.22 months for nivolumab and sitravatinib and 10.58 months for docetaxel. The 95% confidence interval for the combination group's median runs from 10.41 to 13.93 months; for docetaxel, it runs from 9.4 to 12.29 months. The intervals communicate uncertainty in each median estimate. They are not a confidence interval for the difference between medians.

The treatment comparison is more directly summarized by the hazard ratio of 0.86, with a 95% confidence interval from 0.70 to 1.05. The interval spans 1, so it includes the value representing equal relative event rates. It also includes values on both sides of 1, leaving uncertainty about the direction and magnitude of the relative comparison. The reported p-value, 0.144, is consistent with the fact that the interval does not exclude 1 at the corresponding 95% level under the reported analysis.

Confidence intervals are not a guarantee that the true value lies inside the particular interval, and overlapping arm-specific intervals are not a formal test of the between-group contrast. The sponsor-reported hazard ratio and its confidence interval should be used for the primary comparison. The registry record does not report a confidence interval for a difference between the two median estimates.

For secondary outcomes, the arm-specific confidence intervals also show uncertainty in the percentages. The intervals are especially important when reading estimates as percentages, because a point estimate alone can make an outcome appear more precisely known than it is. The recalculated unadjusted comparisons do not account for multiplicity, and their intervals should be interpreted as describing the individual comparisons rather than a family of outcomes.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations use the observed effect as a starting point and show estimates for detecting the full observed effect, 75% of the observed effect, and 50% of the observed effect. For overall survival, the figures are total numbers of events, not participants per arm: 1,381 total events for 80% power and 1,848 for 90% power when planning for the full observed effect; 2,454 and 3,285 total events when planning for 75% of it; and 5,521 and 7,391 total events when planning for 50% of it.

For the binary outcomes, the figures are participants per arm. For objective response, the estimates range from 13,182 participants per arm for 80% power and 17,647 for 90% power when planning for the full observed effect, to 51,911 and 69,493 when planning for 50% of it. For clinical benefit, the corresponding range is 269 and 360 for the full observed effect to 1,018 and 1,363 for 50% of it. For one-year survival, it is 1,089 and 1,457 for the full observed effect to 4,367 and 5,845 for 50% of it.

The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For time-to-event outcomes, the calculation uses the Schoenfeld method and counts total events; for the other outcomes, the figures are participants per arm. The 80% power column describes a design that would have an 80% probability of detecting the assumed effect under those calculation assumptions if that effect were the true one. The 90% column describes the corresponding 90% probability.

Smaller effects require more information to detect with the same power, which is why the illustrations call for larger event counts or participant numbers as the assumed effect is reduced. These are planning illustrations based on observed results, not observed power. The original trial's design assumptions, including its sample-size justification, are not reported in the registry record.

13. How the Sample Size Is Derived

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

Formula

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 = 0.860, so ln(HR) = -0.1508.
2. d = 4 × (1.96 + 0.842)² / [ln(0.860)]² = 1,380.2, rounded up to 1,381 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 <- 0.86                              # 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(3906071)
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 = 1,381 (80% power), 1,848 (90% power)
 75% of observed effect: events = 2,454 (80% power), 3,285 (90% power)
 50% of observed effect: events = 5,521 (80% power), 7,391 (90% power)
Simulated power with 1,381 events: 0.808 (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 2,263 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 577 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 <- 10.58          # control-arm median, months (converted from the posted unit)
hr          <- 0.86          # 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: 1680         p (1-sided)   0.0001
  Events: 623        ~HR at bound   0.7428
    Month: 18    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.86   0.0338
    IA 2: 67%                   Z   2.5114
      N: 2264         p (1-sided)   0.0060
 Events: 1246        ~HR at bound   0.8673
    Month: 28    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.86   0.5603
        Final                   Z   1.9930
      N: 2264         p (1-sided)   0.0231
 Events: 1869        ~HR at bound   0.9119
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.86   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 sponsor-reported primary analysis is the log-rank comparison of overall survival, with a hazard ratio of 0.86, a 95% confidence interval from 0.70 to 1.05, and p = 0.144. The posted median estimates and confidence intervals are also reported through Kaplan-Meier estimation. These sponsor-reported statistics are the appropriate basis for describing the primary analysis.

The calculations based on posted summary statistics are simple, unadjusted recalculations for binary outcomes; they do not provide an alternative reconstruction of the sponsor's time-to-event analysis. For overall survival, a hazard ratio and log-rank result depend on event timing and follow-up information that cannot be recovered from arm-specific medians alone. The registry record reports no discrepancy between the sponsor's result and a recalculation, and the time-to-event interpretation uses the sponsor-reported hazard ratio.

The registry does not list sponsor-reported analyses for the posted objective response, clinical benefit and one-year survival comparisons described by recalculated unadjusted p-values. Those calculations are useful as descriptive comparisons of the posted group summaries, but they should not be attributed to the sponsor or treated as the trial's complete inferential analysis. The record does not report whether these outcomes were part of a formal testing hierarchy.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, comparison, time point or analysis. In general, if each test is considered separately without adjustment, the chance of at least one false-positive finding across the family of tests can be greater than the nominal rate for a single test. Methods such as adjusted significance thresholds or a prespecified testing hierarchy can address this issue, but the registry record does not report such a plan for the secondary outcomes.

The primary outcome is overall survival, and the registry reports one sponsor analysis of the primary comparison using the log-rank method. For the secondary outcomes, the record lists multiple measures, including response, clinical benefit, progression-free survival and adverse events. The registry record does not report how the investigators prioritized secondary endpoints, whether any were confirmatory, or whether p-values were adjusted for multiple testing. The unadjusted recalculated p-values therefore have a more limited inferential role than the primary result.

Overall survival uses the Intent-to-Treat population of all randomized participants, and censoring is defined for participants not recorded as dying on study. The record does not provide equivalent detailed analysis-population and missing-data descriptions for every secondary endpoint. It also does not report sensitivity analyses for alternative missing-data assumptions, or details of how unavailable radiographic assessments were handled. These details are important because missing outcomes can affect both arm-specific estimates and comparisons.

The registry record does not report the trial's original sample-size justification, design assumptions, interim-analysis schedule, or prespecified stopping rules. It does list a termination status, but the reason for termination is not reported in the registry record. Thus, the registry summary does not establish whether the trial ended according to a planned rule, because of an operational decision, or for another reason. No such explanation should be inferred from the status 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: malignant neoplasm progression (8.9%), pneumonia (5.7%), febrile neutropenia (5.1%), pulmonary embolism (3.6%), respiratory failure (2.6%).

The posted safety counts are based on participants at risk in each group. In the nivolumab and sitravatinib group, 128 of 281 participants at risk had a serious adverse event; in the docetaxel group, 102 of 273 participants at risk had a serious adverse event. The registry also reports other adverse events for 275 of 281 and 267 of 273 participants, respectively. These counts describe the posted safety summaries and do not by themselves establish that an event was caused by treatment.

The listed deaths were 202 in the combination group and 209 in the docetaxel group. The record does not establish in this summary whether these deaths were treatment-related; overall survival is separately defined as death from any cause. The most frequently listed serious adverse-event terms include malignant neoplasm progression at 8.9%, pneumonia at 5.7%, febrile neutropenia at 5.1%, pulmonary embolism at 3.6%, respiratory failure at 2.6%, and colitis at 2.5%. The record does not identify these term percentages as a comparison between groups in the listed terms. Counts and event terms should therefore be read descriptively, not as causal or comparative conclusions.

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

The primary result describes a randomized comparison of overall survival between nivolumab plus sitravatinib and docetaxel in the population enrolled in this study. The estimated medians were 12.22 months and 10.58 months, respectively. The sponsor-reported hazard ratio was 0.86, with a 95% confidence interval from 0.70 to 1.05 and p = 0.144. The interval includes 1, so the posted analysis does not establish a clear difference in overall survival between the groups.

This result does not show that the treatments are equivalent. A failure to find a statistically persuasive difference is not proof that the true effects are identical. The confidence interval still permits a range of possible relative event rates. Nor does the point estimate alone prove an advantage for the combination: it is an estimate with uncertainty, and the reported interval crosses the null value.

The secondary results provide additional outcomes but do not override the primary analysis. In particular, an unadjusted result for a secondary endpoint should not be presented as a definitive treatment conclusion when the registry does not report a multiplicity strategy. The response and clinical-benefit outcomes are based on radiographic assessments, while one-year survival is a fixed-time summary; each measures something different from overall survival over the full follow-up period.

The results also apply to the study population and its treatment context: advanced non-squamous non-small cell lung cancer following progression on or after platinum-based chemotherapy and checkpoint inhibitor therapy. The registry record does not establish how well these findings generalize to people outside that population or to different treatment settings. It also does not report the reason the trial was terminated, so the termination status cannot be used as an explanation for the findings.

These statistics are a description of trial data, not medical advice. They do not determine what treatment is appropriate for an individual. The record's estimates and their uncertainty should be considered alongside the full study report and other relevant evidence, which are not characterized by the registry summary alone.

19. Why This Trial Matters Statistically

This trial illustrates why a median comparison and a time-to-event treatment comparison are not the same statistic. The medians summarize the estimated survival time at one point on each curve, while the hazard ratio and log-rank analysis use event timing and follow-up across the study. The arm-specific median estimates alone cannot reproduce the sponsor's reported hazard ratio or test.

It also demonstrates the importance of reading estimates together with their uncertainty. The hazard ratio point estimate is below 1, but its 95% confidence interval ranges from 0.70 to 1.05 and includes 1. The reported p-value is 0.144. A reader who focused only on the point estimate or only on the two medians could overlook the uncertainty in the between-group comparison.

The trial includes multiple secondary outcomes, which makes multiplicity relevant. A nominally notable unadjusted secondary comparison can be less persuasive when the testing strategy is not reported. The record's lack of a stated multiplicity plan, sample-size rationale and interim-analysis details limits what can be concluded about how those analyses were intended to support claims.

Finally, the planning illustrations emphasize that required information depends on the effect one aims to detect. Smaller assumed effects require more events or participants for the same target power under the stated illustrative assumptions. Those calculations are distinct from the original study design, which is not documented in the registry record, and are not a measure of the trial's observed power.

20. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record gives the trial's termination status but not the reason for termination. Without that context, readers cannot infer whether termination followed a planned stopping rule, a sponsor decision, an operational issue or another circumstance. The record also does not report interim analyses or stopping boundaries, so it is not possible to assess how any interim review may have related to the final analysis.

The original sample-size justification and design assumptions are not reported. The planning illustrations based on observed effects are not a substitute for the protocol's original assumptions. The record does not explain whether the enrollment target was selected to detect a particular overall survival effect or to meet a specified power goal.

The primary outcome specifies Kaplan-Meier estimation, the censoring definition and a log-rank comparison, but the registry summary does not provide all participant-level event and censoring information needed to reproduce the time-to-event analysis. It also does not report enough detail in this record to assess the proportional-hazards assumption or alternative time-to-event analyses. These are limitations of the registry summary, not evidence that a particular assumption was violated.

For secondary endpoints, the registry record does not describe adjustment for multiple comparisons, a testing sequence, or detailed missing-data handling. The listed secondary outcomes extend beyond the results described, and the reason results are not reported for every outcome is not stated. The serious adverse-event summary also does not provide enough detail to establish causality for individual events or to interpret the listed term percentages as between-arm comparisons.

Finally, the study population was defined by advanced non-squamous non-small cell lung cancer and prior treatment progression. Generalization to other clinical populations or treatment histories is not established by the registry results alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Phase 3 Study of Sitravatinib Plus Nivolumab vs Docetaxel in Patients With Advanced Non-Squamous Non-Small Cell Lung Cancer — NCT03906071.
• Registry record last updated 2026-09-30; status last verified 2026-08.
• Results first posted 2024-06-25.
• 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.

24. Record Summary

NCT03906071 is a randomized, open-label, phase 3, parallel-group study comparing sitravatinib plus nivolumab with docetaxel in advanced non-squamous non-small cell lung cancer after progression on or after platinum-based chemotherapy and checkpoint inhibitor therapy. The registry lists 577 participants and identifies overall survival as the primary outcome in the Intent-to-Treat population.

Median overall survival was 12.22 months for the combination and 10.58 months for docetaxel. The sponsor-reported hazard ratio was 0.86, with a 95% confidence interval from 0.70 to 1.05 and a log-rank p-value of 0.144. Secondary results include response, clinical benefit, one-year survival and safety outcomes. The registry lists the study as terminated; the reason is not reported in the registry record.