Ramucirumab and Pembrolizumab Versus Standard of Care in Treating Patients With Stage IV or Recurrent Non-small Cell Lung Cancer (A Lung-MAP Non-Match Treatment Trial): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ramucirumab and Pembrolizumab Versus Standard of Care in Treating Patients With Stage IV or Recurrent Non-small Cell Lung Cancer (A Lung-MAP Non-Match Treatment Trial) (NCT03971474), a randomized phase 2 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This was a randomized, open-label, parallel-group phase II trial sponsored by SWOG Cancer Research Network. The registry lists enrollment as 166 and marks the study completed. The study start was 2019-05-28, and primary completion was 2022-04-14. Those dates describe the registry record; they do not supply the timing or results of any interim analyses.

Participants were assigned to investigator-choice standard of care or ramucirumab plus pembrolizumab. Because masking was listed as none, the trial was open-label: treatment assignment was not masked. Open-label assignment can matter when outcomes involve judgments, such as investigator-assessed progression, although the primary outcome of death is less dependent on subjective assessment. The registry does not report further details about procedures intended to limit assessment bias.

The comparator was not a single fixed drug regimen. Docetaxel, gemcitabine and pemetrexed appear in the intervention record, but the standard-of-care arm description is truncated. The posted record therefore does not fully establish which specific regimen each participant received or how treatment selection was distributed.

Overall survival was the primary outcome, measured from registration to death from any cause, with participants last known alive censored at their last contact. The reported analysis population is eligible and evaluable participants. Response rate, disease control rate and investigator-assessed progression-free survival are among the listed secondary outcomes. The registry also lists duration of response, adverse events and subgroup analyses, but the outcome descriptions and analyses are not all represented in the posted results. The trial’s original sample-size justification and detailed analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 166 participants were initially randomized to the study, 82 to the ramucirumab + pembrolizumab (RP) arm and 84 to the standard of care (SOC) arm. 30 were ineligible, 13 in the RP arm and 17 in the SOC arm. In all, 136 participants were eligible and included in the primary analysis (RP n=69, SOC n=67).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Eligible and evaluable 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.

Population: Participants who are eligible and evaluable for the primary analysis

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over From date of registration to a maximum of 2 years and 11 months or death.

Overall survival measures the time from registration until death from any cause. Participants last known to be alive are censored at the date of last contact: their exact later survival time is not observed, but their follow-up contributes information up to that contact. The stated timeframe extends from registration to a maximum of 2 years and 11 months or death.

Survival outcomes are useful when the question concerns how long participants remain alive, because they account for the timing of events and can include participants whose event has not yet been observed. A median summarizes the time by which the estimated survival experience has reached its midpoint; it does not describe every participant’s outcome or the full shape of the survival pattern. The posted medians are 11.6 months for standard of care and 14.5 months for ramucirumab plus pembrolizumab.

The registry also reports a hazard ratio from a Log Rank analysis. In general, a hazard ratio summarizes the relative event rate over follow-up under the analysis assumptions; it is not a comparison of median survival times and should not be interpreted as a direct difference in months. The primary outcome is clinically interpretable, but the registry record does not report the survival curve details, proportional-hazards assessment, or a fuller description of the model used to obtain the reported estimate.

7. Results Posted in the Registry

• Standard of Care (Inv. Choice) vs Ramucirumab + Pembrolizumab: hazard ratio 0.69 (95% CI 0.51–0.92), reported p = 0.050 (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.

Response Rate (RR)

• 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:
  • Ramucirumab + Pembrolizumab: 21.7% (15/69) versus 28.4% (19/67) on control; risk difference -6.6 percentage points (95% CI -21.2 to 7.9), risk ratio 0.77 (0.43–1.38); unadjusted two-proportion z-test p = 0.373.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramucirumab + Pembrolizumab and the control. The interval gives the range of effects that remain compatible with the data.

Disease Control Rate (DCR)

• 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:
  • Ramucirumab + Pembrolizumab: 75.4% (52/69) versus 73.1% (49/67) on control; risk difference 2.2 percentage points (95% CI -12.5 to 16.9), risk ratio 1.03 (0.85–1.26); unadjusted two-proportion z-test p = 0.766.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramucirumab + Pembrolizumab and the control. The interval gives the range of effects that remain compatible with the data.

Investigator Assessed-progression-free Survival (IA-PFS)

• 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:
  • Standard of Care (Inv. Choice) vs Ramucirumab + Pembrolizumab: hazard ratio 0.86 (95% CI 0.66–1.14), reported p = 0.250 (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 Standard of Care (Inv. Choice) vs Ramucirumab + Pembrolizumab and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover distinct dimensions: response and disease control are binary assessments, while investigator-assessed progression-free survival is a time-to-event outcome. Their overall pattern does not provide a single, uniform signal that can be substituted for the primary overall-survival result. Each outcome has its own definition, follow-up, assessment process and uncertainty. For example, investigator assessment may be influenced by open-label treatment assignment, whereas a survival endpoint relies on death and censoring information.

Secondary outcomes can help describe how treatment groups compare beyond the primary endpoint, but they generally carry less confirmatory weight. The registry lists multiple secondary outcomes and subgroup analyses, and reports 14 analyses overall. Testing many outcomes increases the chance of finding a nominally notable result by chance if no adjustment is made. The registry record does not report a multiplicity adjustment or identify a hierarchy governing interpretation of these secondary tests.

Results for secondary endpoints should consequently be read as supportive or exploratory unless the record documents a prespecified confirmatory role and appropriate control of multiplicity. The posted secondary tests include p-values, but a p-value alone does not convey effect size, precision, clinical importance, or the probability that a hypothesis is true. Confidence intervals and outcome definitions are essential to interpretation.

The record lists duration of response, adverse events, subgroup analyses and other endpoints, but not every listed secondary outcome has a complete result described in the posted data. Their absence from the available results should not be read as evidence of no effect. The registry record does not report why particular secondary results are unavailable or whether analyses were omitted, not completed, or not entered. Overall, the secondary outcomes add context to the primary survival comparison but do not resolve the limitations in interpretation or establish a definitive conclusion on their own.

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

• Response Rate (RR)
• Disease Control Rate (DCR)
• Duration of Response (DOR)
• Number of Participants With Gr 3 Through 5 Adverse Events That Are Related to Study Drugs
• Investigator Assessed-progression-free Survival (IA-PFS)
• Overall Survival (OS), Subgroup Analysis by Stratification Factors
• Investigator-Assessed Progression-Free Survival (IA-PFS), Subgroup Analysis by Stratification Factors

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help distinguish the size of an estimate from its uncertainty and clarify what a comparison can support. The registry identifies a Log Rank method for the reported survival comparisons, a hazard ratio as the effect measure, and confidence intervals for the primary outcome and investigator-assessed progression-free survival. It identifies a Chi-squared method for the sponsor-reported response and disease-control tests.

What does a median survival estimate describe?

A median time-to-event estimate is a point on the estimated event-time distribution. For overall survival, the event is death from any cause. A median is useful because it gives a time-based summary while allowing participants with incomplete follow-up to contribute information before censoring. It does not show whether the groups differed consistently throughout follow-up, nor does it reveal the shape of the survival curve. Two groups can have medians that summarize their distributions but still have more complicated patterns at other times.

What does a hazard ratio describe?

A hazard ratio compares event rates between groups over follow-up, under the analysis and assumptions used. It is not a risk ratio, a percentage-point difference, or a difference between medians. The posted primary hazard ratio is 0.69, and the progression-free survival hazard ratio is 0.86. Interpretation depends on how the event and comparison groups were coded. The registry names the group comparison but does not supply a detailed coding explanation or report an assessment of whether the relative event rate was sufficiently stable over time.

The Log Rank method is a general approach for comparing time-to-event experience between groups. It uses information about event timing and censoring rather than reducing all follow-up to a simple count. Its interpretation depends on the study’s follow-up and analysis choices. The registry record identifies the method but does not report all implementation details, such as the exact analysis population for every survival comparison or diagnostics of model assumptions.

How should a confidence interval be read?

A confidence interval expresses uncertainty around an estimate under the method used. The primary outcome has an 80% confidence interval from 0.51 to 0.92 for the reported hazard ratio. The investigator-assessed progression-free survival hazard ratio has an 80% confidence interval from 0.66 to 1.14. An interval is not a range containing every plausible individual outcome; it quantifies uncertainty about a population-level parameter. A wider interval indicates less precision than a narrower interval on the same scale. The confidence level matters: an 80% interval is not the same as a 90% or 95% interval, so confidence intervals should not be compared without noting their stated level.

For binary outcomes such as response rate and disease control rate, a percentage describes the proportion meeting the outcome definition. A risk difference expresses the difference between group proportions on an absolute scale. A risk ratio compares proportions as a ratio, while an odds ratio compares odds. These measures answer related but distinct questions. The posted secondary estimates include confidence intervals and recalculated effect measures, but the registry’s sponsor-reported significance tests use the listed Chi-squared method. The Chi-squared test assesses evidence against a no-association null under its assumptions; it does not explain the size or practical importance of an effect.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability exceeds what a model assumes. If not accounted for, standard errors may be too small and confidence intervals may be too narrow. This concept is relevant to count or clustered data, but the registry does not report an over-dispersion analysis for these outcomes. It should not be assumed that over-dispersion was present or that a particular correction was used.

Likewise, the registry does not report enough detail to establish the assumptions behind all the binary-outcome estimates, the handling of missing outcome data, or any adjustment for covariates. Those omissions limit independent reconstruction. The methods named in the record identify the broad analysis approach, but do not substitute for a complete statistical analysis plan.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the available data and analysis. The primary outcome’s hazard ratio is 0.69, with an 80% confidence interval from 0.51 to 0.92. That interval gives a range of values compatible with the analysis at its stated confidence level; it does not remove uncertainty or establish that the true effect equals the point estimate. Its endpoints are on the hazard-ratio scale, not in months of survival.

The reported median overall survival estimates are 11.6 months and 14.5 months, with 80% confidence intervals of 9.9 to 13.0 months and 13.9 to 16.1 months, respectively. These intervals describe uncertainty in each median estimate. They are not a confidence interval for the difference between medians, and comparing overlap between separate intervals is not a substitute for the reported group comparison.

The progression-free survival hazard ratio has an 80% confidence interval from 0.66 to 1.14, which includes 1. Its medians are reported with intervals from 4.2 to 5.7 months and 4.2 to 6.1 months. The binary secondary outcomes use 90% confidence intervals for the group percentages. Different confidence levels and outcome scales make direct comparisons of interval widths inappropriate.

Precision is limited by the amount of information available for each analysis and by follow-up, censoring, event frequency and the analysis method. The registry does not report all details needed to evaluate those contributions. A confidence interval can describe statistical uncertainty under the stated analysis, but it does not account for every possible bias, missing-data issue, or limitation in generalizing results to other populations.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. For binary outcomes, the displayed figures are participants per arm. For time-to-event outcomes, they are total events, not participants. These distinctions matter: an event target is not a recruitment target, and the number of participants needed to observe a given number of events depends on follow-up and event occurrence.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The 80% power column gives the illustrated sample size or event target for a design with 80% power under those assumptions. The 90% power column gives the corresponding target for 90% power. Power is the probability, under a specified effect and model, of rejecting the null hypothesis at the chosen significance level. It is a design property, not the probability that a result is true.

Rows that plan for a smaller fraction of the observed effect require more information than rows based on the full observed effect. That is because smaller effects are harder to distinguish from random variation. The resulting illustrations can become very large, particularly for outcomes with small observed contrasts. They should not be read as recommendations or as evidence that the trial was designed to those targets. The original design assumptions and sample-size justification are not reported in the registry record. These figures are 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 = 0.690, so ln(HR) = -0.3711.
2. d = 4 × (1.96 + 0.842)² / [ln(0.690)]² = 228.0, rounded up to 229 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 <- 0.69                              # 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(3971474)
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 = 229 (80% power), 306 (90% power)
 75% of observed effect: events = 406 (80% power), 543 (90% power)
 50% of observed effect: events = 913 (80% power), 1,222 (90% power)
Simulated power with 229 events: 0.790 (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 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 166 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 <- 11.6          # control-arm median, months (converted from the posted unit)
hr          <- 0.69          # 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: 310         p (1-sided)   0.0001
 Events: 103        ~HR at bound   0.4805
   Month: 19    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.69   0.0338
   IA 2: 67%                   Z   2.5114
      N: 396         p (1-sided)   0.0060
 Events: 205        ~HR at bound   0.7041
   Month: 30    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.69   0.5603
       Final                   Z   1.9930
      N: 396         p (1-sided)   0.0231
 Events: 308        ~HR at bound   0.7967
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.69   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’s own analysis is the primary record of the trial’s reported inferential results. For overall survival, the registry reports a Log Rank hazard ratio of 0.69, an 80% confidence interval from 0.51 to 0.92, and p = 0.05. For investigator-assessed progression-free survival, it reports a hazard ratio of 0.86, an 80% confidence interval from 0.66 to 1.14, and p = 0.25. The posted recalculations do not independently reproduce those time-to-event analyses; they use the sponsor-reported hazard ratios where that is the specified approach.

For the binary outcomes, the simple recalculations use posted group summaries and are unadjusted. The recalculated response-rate comparison has p = 0.373, while the registry’s Chi-squared analysis reports p = 0.19. The recalculated disease-control comparison has p = 0.766, while the registry reports p = 0.38. These are not interchangeable analyses: differences can reflect methods, rounding, or data handling, and the registry record does not explain the differences. The recalculations are useful as transparent checks on the posted summaries, not replacements for the sponsor’s analyses.

The registry also includes additional superiority-test rows for overall survival and progression-free survival with p = 0.15 and p = 0.14, respectively, without corresponding estimates or method details in those rows. Their relationship to the fully described analyses is not reported in the registry record. The interpretations should therefore distinguish the specified sponsor analyses from these incompletely described entries.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, subgroups or analyses are tested. If each test is interpreted without accounting for the others, the chance of at least one apparently positive result can increase. This is a general statistical concern, especially when a trial includes primary and secondary outcomes and subgroup analyses. The registry lists several secondary outcomes and 14 analyses, but does not report a multiplicity-control strategy, a testing hierarchy, or which analyses were designated confirmatory. It is therefore not possible to determine from the registry record whether the reported p-values were adjusted or how the analyses were prioritized.

The record identifies the primary analysis population as eligible and evaluable participants. It does not provide enough detail to establish how eligibility and evaluability were determined, whether all randomized participants were included in each analysis, or how deviations from assigned treatment were handled. An intention-to-treat analysis is not described in the registry record. These details matter because analysis populations can affect comparability between randomized groups.

Missing data are also not described in sufficient detail. For overall survival, participants last known alive are censored at their date of last contact. That is part of the stated endpoint definition, but the registry does not report the amount or pattern of loss to follow-up, missing covariate or outcome data, or any sensitivity analyses for informative censoring. It does not report how missing assessments were handled for response, disease control or investigator-assessed progression-free survival.

These gaps do not establish that the analysis was inappropriate; they limit what can be verified from the posted record. Without the prespecified statistical analysis plan, multiplicity procedures, missing-data details and complete analysis-population definitions, the reported results are best interpreted as the registry presents them, with caution about the strength of secondary and subgroup evidence.

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: lung infection (10.1%), dyspnea (10.1%), hypoxia (8.7%), sepsis (7.2%), respiratory failure (7.2%).

The registry’s safety figures list serious adverse events among participants at risk: 11 of 60 in the standard-of-care group and 28 of 69 in the ramucirumab-plus-pembrolizumab group. These are counts within the reported at-risk groups; they should not be converted into a causal comparison without further detail about event definitions, follow-up and analysis. The record separately lists other adverse events affecting 60 of 60 and 69 of 69 participants. The meaning and collection rules for these categories are not fully described in the posted data.

The most frequently listed serious terms include lung infection and dyspnea, each at 10.1%, followed by hypoxia at 8.7%, and sepsis, respiratory failure and hypertension, each at 7.2%. These percentages describe reported terms and are not necessarily mutually exclusive: a participant may experience more than one event. The registry does not provide enough detail to interpret them as rates of unique participants or to compare each term across groups.

Deaths are listed as 51 and 45 in the respective groups. The record does not state in this safety summary that these deaths were caused by treatment. Serious adverse event counts, adverse event terms and deaths are distinct measures and should not be conflated.

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

The results describe outcomes observed in a randomized phase II trial among eligible and evaluable participants with stage IV or recurrent non-small cell lung cancer previously treated with immunotherapy. The primary outcome is overall survival. Its posted medians and reported hazard ratio provide a statistical comparison between investigator-choice standard of care and ramucirumab plus pembrolizumab, with uncertainty expressed through confidence intervals and a reported p-value.

These estimates do not establish that treatment caused a difference. Randomization supports comparison, but interpretation still depends on the analysis population, follow-up, censoring, measurement and assumptions. The open-label design and incomplete information about treatment selection and analysis procedures are relevant limitations. The registry record does not provide a complete statistical analysis plan or enough detail to resolve every methodological question.

The results also do not prove that the observed estimates would apply to every patient with this diagnosis, to people treated in other settings, or to other treatment choices. The comparator was investigator choice rather than one uniform regimen, and the posted description is incomplete. The registry does not provide a basis for comparing each component of that standard-of-care choice separately.

Secondary outcomes add descriptive context but should not replace the primary endpoint. They include outcomes with different definitions and uncertainty, and the record does not report multiplicity control. Safety counts describe reported adverse events, not necessarily events caused by study treatment. Overall, the record supports careful description of the estimates and their precision; it does not support medical advice or a universal claim that either regimen works or does not work.

19. Why This Trial Matters Statistically

This trial is statistically informative because it compares a combination regimen with investigator-choice standard of care using random assignment and a time-to-event primary endpoint. Overall survival incorporates event timing and censoring, making the analysis different from a simple comparison of the number of deaths observed at a single point. The reported hazard ratio and confidence interval allow readers to consider both the estimated contrast and its uncertainty.

The record also illustrates why outcomes should not be treated as interchangeable. Overall survival, investigator-assessed progression-free survival, response rate and disease control capture different features of the clinical course. Their estimates need not align, and a secondary endpoint cannot simply confirm or contradict the primary endpoint. The open-label design is particularly relevant when an outcome depends on investigator assessment.

The posted planning illustrations make another important statistical point: smaller effects require more information to detect under the stated assumptions. They are based on the observed effects and are not the original design rationale. This distinction prevents planning calculations from being mistaken for evidence about what the completed trial was capable of detecting.

Finally, the record shows the importance of transparent reporting. Confidence levels, analysis populations, multiplicity, missing-data handling and the exact statistical plan all affect interpretation. Some of these details are not reported, so the conclusions should remain proportionate to the available estimates. The trial is most useful as a specific randomized comparison whose results can be examined with attention to endpoint definition, precision and limits on independent verification.

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 leaves several trial-specific uncertainties. It describes the standard-of-care comparator as investigator choice and lists docetaxel, gemcitabine and pemetrexed, but the arm description is truncated. This limits understanding of the actual treatment mix and makes the comparator less straightforward to interpret than a single fixed regimen.

The primary outcome population is described as eligible and evaluable participants, but the registry does not explain the criteria for evaluability or how the analysis population relates to all randomized participants. Detailed follow-up information, numbers censored over time, survival curves and sensitivity analyses are not reported in the available record. The stated censoring rule for participants last known alive does not by itself show whether censoring was independent of prognosis.

The trial is open-label, and investigator-assessed progression-free survival may be susceptible to assessment differences. The registry does not report blinded central review or other procedures used to address this possibility. It also does not report an assessment of assumptions for the survival comparisons, complete missing-data procedures, a multiplicity plan, or the original sample-size justification. The extra superiority-analysis rows for survival outcomes do not have full method or estimate details.

Safety reporting is limited in the posted summary. Serious-event counts and selected terms are listed, but definitions, follow-up windows and attribution details are not fully described. The registry does not explain the incomplete outcome reporting for all listed secondary endpoints. These limitations constrain independent appraisal and should be kept distinct from the observed point estimates themselves.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Ramucirumab and Pembrolizumab Versus Standard of Care in Treating Patients With Stage IV or Recurrent Non-small Cell Lung Cancer (A Lung-MAP Non-Match Treatment Trial) — NCT03971474.
• Registry record last updated 2024-09-03; status last verified 2024-08.
• Results first posted 2023-04-25.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

NCT03971474 is a completed, randomized, open-label, parallel-group phase II trial sponsored by SWOG Cancer Research Network. It studied ramucirumab plus pembrolizumab versus investigator-choice standard of care in patients with stage IV or recurrent non-small cell lung cancer previously treated with immunotherapy. The registry lists enrollment as 166.

Overall survival was the primary outcome, measured from registration to death from any cause. The registry reports medians of 11.6 months for standard of care and 14.5 months for the combination, and a Log Rank hazard ratio of 0.69 with an 80% confidence interval from 0.51 to 0.92 and p = 0.05. Secondary outcomes include response, disease control and investigator-assessed progression-free survival. Missing detail about the analysis plan, multiplicity, missing data and comparator treatment mix limits independent interpretation.