Evaluation Of The Efficacy Of The Combination Of Axitinib With Pemetrexed And Cisplatin In The Treatment Of Non-Squamous Non-Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation Of The Efficacy Of The Combination Of Axitinib With Pemetrexed And Cisplatin In The Treatment Of Non-Squamous Non-Small Cell Lung Cancer (NCT00768755), a randomized phase 1, phase 2 study. The primary outcome is Progression-Free Survival (PFS).

2. Clinical Question

3. Trial Design

The registry describes a randomized, unmasked study with phase 1 and phase 2 components and a recorded enrollment of 180. Its official title identifies the phase 2 comparison as cisplatin and pemetrexed with or without axitinib for first-line treatment of non-squamous non-small cell lung cancer. The registry status is completed. Start and primary completion are recorded as 2009-01 and 2011-03.

Five arm descriptions appear in the record, including phase 1 treatment and several axitinib schedules. The primary outcome results, however, are posted for three phase 2 groups: continuous axitinib with pemetrexed and cisplatin, modified axitinib with pemetrexed and cisplatin, and pemetrexed and cisplatin alone. The phase 2 arm summaries report 55, 58, and 57 participants, respectively. These arm-specific results should not be confused with the registry-wide enrollment figure.

The primary analysis population included randomized participants according to their initial medication assignment, whether or not they received the assigned study medication. This is an intention-to-treat-style assignment principle, although the registry calls it the full analysis population. The endpoint description does not specify a separate adherence-based or treatment-received analysis.

The allocation method is recorded as randomized and masking as none. Further details about sequence generation, concealment, stratification, and the reasons for the tested axitinib schedules are not reported in the registry record. The trial's original sample-size justification and detailed analysis plan are also not reported in the registry record. The planning illustrations associated with the posted results are calculations based on observed effects, not a substitute for those original design details.

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.

Phase 1

Reasons for not completing this period:

Phase 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis (FA) population, included all participants randomized with study medication assignment designated according to initial randomization, regardless of whether participants received study medication or received a different drug from that to which they were randomized.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS), measured over Phase 2 baseline until the date of first documented progression or death due to any cause or initiation of subsequent anticancer therapy, assessed every 6 weeks up to 84 weeks.

Progression-free survival measures the time from randomization until the first recorded event among objective tumor progression, death from any cause, or initiation of subsequent anticancer therapy. The registry defines the endpoint as time in months and reports the median and a 95% confidence interval for each arm. Tumor progression was determined from oncologic assessment data meeting the criteria for progressive disease. Death was identified from adverse-event data with an outcome of death or from end-of-study data.

The registry says progression-free survival was assessed every 6 weeks up to 84 weeks. This makes the endpoint a time-to-event outcome: participants may have different lengths of follow-up, and some may have no recorded event during the observation period. A median is the time by which half of the relevant event-time distribution has occurred, rather than an average duration. It gives an interpretable summary, but it does not describe the full pattern of event timing or the uncertainty in every part of the survival curve.

Progression-free survival is commonly used in clinical trials because it combines tumor progression and death into a defined endpoint that can be observed before overall survival is fully known. That is a general explanation of the endpoint's role, not a claim about the rationale documented for this trial. The registry record does not report a specific rationale for selecting progression-free survival as the primary endpoint.

7. Results Posted in the Registry

• Axitinib (Continuous) + Pemetrexed/Cisplatin (Phase 2) vs Pemetrexed/Cisplatin (Phase 2): hazard ratio 0.83 (95% CI 0.51–1.36), reported p = 0.304 (as reported in the registry).
• Axitinib (Modified) + Pemetrexed/Cisplatin (Phase 2) vs Pemetrexed/Cisplatin (Phase 2): hazard ratio 0.95 (95% CI 0.58–1.55), reported p = 0.356 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Overall Survival (OS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Axitinib (Continuous) + Pemetrexed/Cisplatin (Phase 2) vs Pemetrexed/Cisplatin (Phase 2): hazard ratio 1.05 (95% CI 0.65–1.69), reported p = 0.579 (as reported in the registry).
  • Axitinib (Modified) + Pemetrexed/Cisplatin (Phase 2) vs Pemetrexed/Cisplatin (Phase 2): hazard ratio 1.45 (95% CI 0.92–2.29), reported p = 0.939 (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 Axitinib (Continuous) + Pemetrexed/Cisplatin (Phase 2) vs Pemetrexed/Cisplatin (Phase 2) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Axitinib (Modified) + Pemetrexed/Cisplatin (Phase 2) vs Pemetrexed/Cisplatin (Phase 2) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Objective Response (OR)

• 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:
  • Axitinib (Modified) + Pemetrexed/Cisplatin (Phase 2): 39.7% (23/58) versus 45.5% (25/55) on control; risk difference -5.8 percentage points (95% CI -24.0 to 12.4), risk ratio 0.87 (0.57–1.34); unadjusted two-proportion z-test p = 0.533.
  • Pemetrexed/Cisplatin (Phase 2): 26.3% (15/57) versus 45.5% (25/55) on control; risk difference -19.1 percentage points (95% CI -36.6 to -1.7), risk ratio 0.58 (0.34–0.98); unadjusted two-proportion z-test p = 0.035.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Axitinib (Modified) + Pemetrexed/Cisplatin (Phase 2) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Pemetrexed/Cisplatin (Phase 2) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover overall survival, objective response, duration of response, and changes in symptom severity and symptom interference. Across the outcomes with numerical results posted, the findings are not uniform: the overall-survival comparisons do not establish a clear separation, while the objective-response comparisons differ in how strongly they distinguish the axitinib groups from chemotherapy alone. This variation is a reason to avoid treating any single secondary finding as a complete account of the trial.

The registry lists duration of response and the two MDASI symptom measures, but their numerical results are not reported in the registry record. The record therefore does not support a quantitative account of their direction, magnitude, or precision. The secondary findings can provide context for the primary progression-free survival result, but they do not replace it or resolve the uncertainty in the primary comparisons.

Secondary analyses are often less persuasive when many outcomes and comparisons are examined without a reported multiplicity adjustment. General explanation: the more statistical tests performed, the greater the opportunity for at least one apparently notable result to arise by chance. The registry record does not report a multiplicity strategy or identify which secondary hypotheses, if any, were confirmatory. Accordingly, secondary results should be interpreted as supportive or exploratory unless the full protocol and analysis plan establish otherwise.

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

• Overall Survival (OS)
• Percentage of Participants With Objective Response (OR)
• Duration of Response (DR)
• Change From Baseline in Monroe Dunaway (MD) Anderson Symptom Inventory (MDASI) Symptom Severity Score
• Change From Baseline in Monroe Dunaway (MD) Anderson Symptom Inventory (MDASI) Symptom Interference Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time-to-event data. Each participant contributes information about time from randomization to the defined event or, if no event is recorded, to the end of available observation. General explanation: time-to-event methods are useful when follow-up can differ between participants and when some observations are censored, meaning the event has not been observed by the end of a participant's recorded follow-up. The registry record does not describe the censoring rules in detail.

What does the median summarize?

The median progression-free survival is a point on the event-time distribution: it marks the time by which half of the distribution has experienced the event. It is not the mean follow-up time, nor does it indicate how long every participant remained progression-free. A median can be useful for communicating an arm's outcome, but it compresses the time-to-event curve into one number. The reported confidence interval expresses uncertainty around that median estimate.

How should a hazard ratio be read?

The sponsor reported hazard ratios from log-rank analyses for the two comparisons. A hazard ratio compares event rates over follow-up, rather than comparing only the two median values. General explanation: the hazard is the instantaneous event rate among participants still at risk at a given time. A hazard ratio below 1 indicates an estimated lower hazard in the first group named in the comparison, while a value above 1 indicates an estimated higher hazard. This interpretation depends on the treatment ordering and does not mean that the same relative difference applies to every participant or every point in time.

The reported hazard ratios are 0.831 and 0.947 for the continuous and modified axitinib comparisons, respectively. Their confidence intervals extend across 1. The registry reports p-values of 0.304 and 0.356. Together, the estimates and uncertainty do not provide a statistically clear separation in the primary comparisons. A p-value measures how incompatible the observed data are with a specified null model under the test's assumptions; it is not the probability that the null hypothesis is true and it does not measure clinical importance.

What does the confidence interval contribute?

A 95% confidence interval gives a range of values compatible with the data under the method used, with a coverage interpretation over repeated use of that method. It is not a guarantee that the true effect lies in the particular interval, nor does it mean that 95% of participants had outcomes inside that range. For the hazard ratios, the intervals show substantial uncertainty around the point estimates. Because they include 1, the data do not rule out no relative hazard difference at the conventional level associated with these intervals.

For the arm medians, the intervals quantify uncertainty in each median separately. They should not be treated as a direct interval for the difference between medians. A direct contrast requires a method that accounts for the comparison and the time-to-event data. The registry's reported log-rank analyses are the available sponsor comparisons; a separate adjusted analysis is not reported in the registry record.

How do the response analyses differ?

Objective response is a binary outcome: each participant is classified according to whether an objective response was recorded under the endpoint definition. The registry reports arm percentages with confidence intervals and sponsor risk ratios from Cochran-Mantel-Haenszel analyses. A risk ratio compares the probability of response between groups. The separate simple recalculations based on posted counts are unadjusted comparisons and are not the sponsor's analyses. General explanation: an adjusted or stratified comparison can differ from a raw comparison when it accounts for grouping factors or uses a different analysis method. The registry record does not provide enough detail to infer which factors were used in the sponsor's calculation.

The recalculated risk differences and p-values are therefore best read as supplementary, unadjusted summaries, not replacements for the sponsor-reported results. They compare the posted response proportions directly and do not necessarily reproduce a method that accounts for stratification or other design features. The sponsor's own analysis takes precedence if a discrepancy is identified; the record indicates no discrepancy for this analysis.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variability exceeds what a statistical model assumes. It can make standard errors too small and confidence intervals too narrow if the model does not allow for the extra variability. The registry does not report an over-dispersion assessment for the primary time-to-event outcome, and this issue should not be inferred from the posted summaries. Different outcomes call for different statistical models; over-dispersion is not a universal concern for every endpoint.

The registry identifies the primary analysis population and the reported methods, but not the full statistical analysis plan. Details such as handling of missing endpoint assessments, censoring specifications, prespecified covariates, and planned interim analyses are not reported in the registry record. Those omissions limit how fully an outside reader can reproduce or audit the analyses.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. For progression-free survival, the arm-specific median confidence intervals are 6.7 to 10.0 months for continuous axitinib, 6.8 to 9.9 months for modified axitinib, and 5.8 to 9.4 months for pemetrexed and cisplatin. These ranges show that the medians are estimated with uncertainty; a point estimate alone would understate that uncertainty.

The treatment-comparison intervals are especially important for interpretation. The continuous-axitinib hazard ratio is 0.831, with a 95% confidence interval of 0.508 to 1.360. The modified-axitinib hazard ratio is 0.947, with a 95% confidence interval of 0.580 to 1.546. Both intervals include 1, the value corresponding to no relative hazard difference. Their widths also show that the data are compatible with a range of relative effects, not just the point estimates.

A confidence interval is not a measure of the probability that the result will be reproduced, and the 95% label does not imply that 95% of participants' outcomes fall within the interval. It describes the statistical uncertainty under the analysis method. General explanation: more information can improve precision, but precision also depends on event occurrence, follow-up, variability, and the analysis design. The registry does not report enough detail to attribute the width of these intervals to any one factor.

Overlap between arm-specific median intervals is not itself the formal test of a treatment difference. Conversely, an interval that includes the no-effect value does not prove equivalence. Equivalence or non-inferiority requires a prespecified margin and an analysis designed to evaluate it; such a margin is not reported in the registry record.

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 translate an observed effect into hypothetical sample-size requirements under stated assumptions. For time-to-event outcomes, the entries are total events, not participants per arm. For the objective-response outcome, the entries are participants per arm. The units differ, so values from the time-to-event planning rows should not be compared directly with the response planning rows.

The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect. The 80% power column describes a hypothetical design with an 80% chance of rejecting the null under the assumed effect and model; the 90% column uses a higher target probability under those same assumptions. These are planning illustrations, not observed power.

The row for the full observed effect uses the effect estimated in this trial as its planning target. The rows for 75% and 50% of the observed effect represent smaller target effects. Smaller effects are harder to distinguish from random variation and therefore require more information, expressed as more participants per arm for response or more total events for time-to-event outcomes. This relationship is a general design principle, not evidence that the trial was designed around those targets.

The registry record does not report the original trial sample-size assumptions or justification. The illustrations should not be read as the number recruited, the number analyzed, or a recommendation for a future study without considering the clinical question and the design assumptions. They also rely on observed effects, which can be unstable, especially when estimates are imprecise.

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 = 0.831, so ln(HR) = -0.1851.
2. d = 4 × (1.96 + 0.842)² / [ln(0.831)]² = 916.1, rounded up to 917 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 <- 0.831                              # 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(768755)
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 = 917 (80% power), 1,227 (90% power)
 75% of observed effect: events = 1,629 (80% power), 2,181 (90% power)
 50% of observed effect: events = 3,665 (80% power), 4,906 (90% power)
Simulated power with 917 events: 0.795 (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 1,396 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 180 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 <- 7.1          # control-arm median, months (converted from the posted unit)
hr          <- 0.831          # 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: 926         p (1-sided)   0.0001
  Events: 414        ~HR at bound   0.6942
    Month: 16    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.83   0.0338
    IA 2: 67%                   Z   2.5114
      N: 1396         p (1-sided)   0.0060
  Events: 827        ~HR at bound   0.8397
    Month: 25    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.83   0.5603
        Final                   Z   1.9930
      N: 1396         p (1-sided)   0.0231
 Events: 1240        ~HR at bound   0.8930
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.83   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

For the primary endpoint, the posted analyses are the sponsor-reported log-rank hazard ratios. The continuous-axitinib comparison reports a hazard ratio of 0.831, a 95% confidence interval of 0.508 to 1.360, and p = 0.304. The modified-axitinib comparison reports a hazard ratio of 0.947, a 95% confidence interval of 0.580 to 1.546, and p = 0.356. These are the analyses to use when describing the registry's primary comparisons; the accompanying planning illustrations do not replace them.

For overall survival, the registry likewise reports sponsor log-rank hazard ratios. For objective response, the sponsor reports risk ratios from Cochran-Mantel-Haenszel analyses. The simple recalculations use posted summary counts and are unadjusted, so their estimands and methods may differ from the sponsor's reported analysis. The registry indicates no discrepancy flag. In general, when a discrepancy is identified between a recalculation and the sponsor's analysis, the sponsor's own analysis takes precedence.

The sponsor-reported methods are stated in the record, but the full specification of the analyses is not. Details about any stratification variables, covariate adjustment, censoring rules, or multiplicity procedure are not reported in the registry record. This limits independent reproduction of the sponsor results.

16. Multiplicity, Missing Data and Analysis Populations

The record lists one primary outcome and several secondary outcomes, with multiple treatment comparisons for some outcomes. It does not report whether the trial controlled the overall type I error across those comparisons, whether a hierarchical testing sequence was prespecified, or whether any secondary analyses were designated as confirmatory. These details are not reported in the registry record.

Multiplicity matters because repeated testing increases the chance of observing at least one small p-value even if there is no true effect across the tested hypotheses. General explanation: a multiplicity procedure can control that risk by adjusting thresholds or by specifying an ordered testing plan. Without a reported strategy, a nominal p-value for a secondary result should not be interpreted as if it were the sole prespecified test.

The primary analysis population is described as the full analysis population, comprising randomized participants assigned according to initial randomization regardless of treatment received. This clarifies the assignment basis for the primary endpoint. The registry does not report detailed missing-data handling, rules for censoring, or sensitivity analyses addressing missing endpoint observations. It also does not report planned interim analyses or the original statistical analysis plan. No assumptions about these procedures should be inferred from the posted estimates.

Because the record is limited on these points, readers cannot fully assess how incomplete assessments, discontinuation, or subsequent treatment were handled beyond the endpoint descriptions. This is an interpretive limitation, not evidence that any particular procedure was or was not used.

17. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: respiratory tract infection (10.0%), vomiting (9.1%), nausea (7.3%), dehydration (5.5%), chest pain (3.6%).

The safety summary reports serious adverse events and other adverse events for phase 1 and phase 2 groups. In the phase 2 continuous-axitinib group, 19 participants were reported with serious adverse events among 55 at risk; in the modified-axitinib group, the corresponding figures were 20 and 58. In the chemotherapy group, 13 participants were reported with serious adverse events among 55 at risk. These are counts, not estimates of comparative risk adjusted for follow-up or other factors.

Other adverse events were reported for 54 of 55 in the continuous-axitinib group, 56 of 58 in the modified-axitinib group, and 54 of 55 in the chemotherapy group. The phase 1 group is listed separately, with 1 of 10 participants reported with serious adverse events and 10 of 10 with other adverse events. The registry lists respiratory tract infection, vomiting, nausea, dehydration, chest pain, and pneumonia among the leading serious adverse-event terms, with percentages reported for each.

These summaries do not establish whether an event was caused by treatment, and the record does not report a comparative safety analysis in the fields summarized. Death counts are not reported in the registry record. Differences in treatment exposure and follow-up can also affect simple event counts, and detailed exposure-adjusted analyses are not reported in the registry record.

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

The primary result is a set of uncertain estimates for progression-free survival in three phase 2 groups. The arm medians are close in the posted summaries, and neither sponsor-reported hazard-ratio comparison provides a statistically clear separation from chemotherapy alone. This describes what the registry analyses show; it does not establish that the regimens are equivalent or that no potentially meaningful effect exists.

The confidence intervals are important to that distinction. They include the no-relative-hazard-difference value and span effects in both directions. The point estimates alone should not be treated as definitive evidence. A non-significant result is not proof of no effect, just as an estimate favoring one direction is not proof that the treatment causes that effect.

Secondary findings do not form a single consistent pattern, and some listed secondary outcomes lack numerical results in the registry. The response analyses offer additional information, but they are secondary and multiple comparisons may affect how much weight they deserve. Overall-survival analyses do not establish a clear difference in the sponsor-reported comparisons. Without a reported multiplicity plan and complete detail on the analyses, these results should be interpreted cautiously.

The registry record cannot answer every question relevant to interpretation. It does not report the original sample-size justification, detailed missing-data procedures, a full statistical analysis plan, or numerical results for every listed secondary outcome. The treatment schedules and population studied also define the scope of the findings. These limitations mean the posted results should be read as trial-specific evidence rather than a universal conclusion about treatment for non-small cell lung cancer.

Nothing in these statistical summaries is medical advice. They describe estimates, uncertainty, and the scope of the available registry record; clinical decisions require evidence and context beyond these analyses.

19. Why This Trial Matters Statistically

This trial is statistically informative because it compares two axitinib schedules with a chemotherapy-only group and reports both arm-level progression-free survival summaries and sponsor-reported time-to-event comparisons. The distinction between a median and a hazard ratio is useful: medians describe one point in each arm's event-time distribution, while hazard ratios summarize a relative event rate over follow-up.

The results also illustrate why uncertainty matters more than a quick comparison of point estimates. The primary hazard-ratio intervals include 1 and are broad enough to encompass effects in more than one direction. Reporting the intervals alongside the p-values prevents the estimates from being reduced to a binary label of significant or not significant.

The record offers a useful contrast between sponsor analyses and simple recalculations for a binary secondary outcome. The sponsor's method and the unadjusted summary answer related but not necessarily identical statistical questions. Recognizing the distinction helps prevent a recalculated result from being mistaken for the trial's prespecified analysis.

Finally, the record shows the limits of registry reporting. The trial's analysis population is stated, but details about multiplicity, missing data, and the original design justification are not. Statistical interpretation depends not only on numerical estimates but also on knowing how analyses were planned, which hypotheses were primary, and how incomplete observations were handled.

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 primary outcome is reported with arm medians and sponsor-reported hazard ratios, but the record does not provide a full survival analysis specification. Censoring rules, detailed assessment handling, and any covariate or stratification factors are not reported in the registry record. These omissions limit independent reproduction and make it difficult to evaluate the sensitivity of the primary result to alternative assumptions.

The registry describes multiple arm schedules, but primary results are posted for three phase 2 groups. The axitinib schedule interrupted before each chemotherapy cycle appears in the arm descriptions but is not among the three primary-result arms. The record does not explain the relationship between all listed arms and the reported phase 2 comparisons in further detail.

The registry lists five secondary outcomes, but numerical results are not reported for duration of response or the symptom severity and symptom interference measures. Multiplicity procedures are also not reported. This restricts assessment of how the collection of secondary analyses should be interpreted and whether any were intended to support confirmatory conclusions.

Safety summaries are counts by group, without a reported comparative analysis in the information summarized. The record does not report deaths in the safety fields, and the listed event counts do not by themselves account for differences in exposure or follow-up. The original sample-size justification and detailed statistical analysis plan are not reported in the registry record. These limitations are specific to the available trial record and should not be filled in by assumptions.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Evaluation Of The Efficacy Of The Combination Of Axitinib With Pemetrexed And Cisplatin In The Treatment Of Non-Squamous Non-Small Cell Lung Cancer — NCT00768755.
• Registry record last updated 2015-10-28; status last verified 2015-10.
• Results first posted 2012-03-30.
• 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

The registry describes a completed randomized, unmasked phase 1 and phase 2 study of axitinib with pemetrexed and cisplatin for non-squamous non-small cell lung cancer. The posted primary results compare continuous axitinib and modified axitinib schedules with pemetrexed and cisplatin alone in the phase 2 groups.

The primary endpoint was progression-free survival. Sponsor-reported hazard ratios for both comparisons have 95% confidence intervals that include 1, and the analyses do not establish a statistically clear difference. Secondary results are mixed, and numerical findings for some listed outcomes are not reported in the registry record. Important details about the original design assumptions, multiplicity, missing data, and the full statistical analysis plan are also not reported in the registry record.