Pembrolizumab/Vibostolimab Coformulation (MK-7684A) or Pembrolizumab/Vibostolimab Coformulation Plus Docetaxel Versus Docetaxel for Metastatic Non Small Cell Lung Cancer (NSCLC) With Progressive Disease After Platinum Doublet Chemotherapy and Immunotherapy (MK-7684A-002, KEYVIBE-002): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pembrolizumab/Vibostolimab Coformulation (MK-7684A) or Pembrolizumab/Vibostolimab Coformulation Plus Docetaxel Versus Docetaxel for Metastatic Non Small Cell Lung Cancer (NSCLC) With Progressive Disease After Platinum Doublet Chemotherapy and Immunotherapy (MK-7684A-002, KEYVIBE-002) (NCT04725188), a randomized phase 2 study. The primary outcome is Progression Free Survival (PFS) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1) by Blinded Independent Central Review (BICR) Assessment.

2. Clinical Question

3. Trial Design

KEYVIBE-002 (NCT04725188) was a phase 2, multicenter, randomized, double-blind, parallel-group study. It enrolled 255 participants and is recorded as completed. The listed start date is 2021-04-20, and the primary completion date is 2023-01-26. The sponsor was Merck Sharp & Dohme LLC. The registry record does not report the original sample-size justification or the detailed randomization procedures.

Participants were assigned to one of three regimens: pembrolizumab/vibostolimab coformulation plus docetaxel; pembrolizumab/vibostolimab coformulation alone; or placebo plus docetaxel. The coformulation contains pembrolizumab and vibostolimab. The arm descriptions specify intravenous administration every three weeks, with treatment planned for up to 35 cycles and approximately 2 years. Docetaxel was specified at 75 mg/m^2 every three weeks in the two arms that included it. Each cycle was described as 21 days.

The primary outcome was progression-free survival (PFS) assessed by blinded independent central review under RECIST 1.1. The registry record defines PFS as time from randomization to first documented progression or death from any cause, whichever occurred first. The reported timeframe was up to approximately 21 months. The primary outcome results are reported for all randomized participants, and the arm-level entries give 87.0, 83.0 and 85.0 participants, respectively. The posted results also include objective response rate, overall survival, duration of response and safety outcomes. The registry record does not report further detail on masking procedures, allocation concealment, adherence, or protocol deviations.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized 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 Progression Free Survival (PFS) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1) by Blinded Independent Central Review (BICR) Assessment, measured over Up to approximately 21 months.

Progression-free survival measures the time from randomization until the first documented disease progression or death from any cause, whichever occurs first. In this study, progression was assessed using RECIST 1.1 by blinded independent central review. This endpoint therefore combines two clinically important events into a time-to-event outcome: disease progression documented by the specified criteria, and death before documented progression.

Time-to-event methods are used because participants can have different lengths of follow-up, and some may not experience the event during the observation period. The analysis can incorporate the time at which an event occurs and account for participants whose event time is not observed before follow-up ends, subject to the assumptions and censoring methods used. Those detailed methods are not reported in the registry record.

The median PFS describes the point in the estimated event-time distribution at which half the observed population's estimated event-free time lies on either side. It is a summary of the distribution, not a statement that every participant experienced progression or death at that time. A hazard ratio compares event rates over follow-up under a model; it is not the ratio of the medians. The posted primary outcome is thus presented both through arm-specific median estimates with confidence intervals and sponsor-reported Cox-model hazard ratios for the two comparisons.

As a general point, a blinded central review can reduce the possibility that knowledge of treatment assignment influences assessment of radiographic progression. The registry record identifies blinded independent central review but does not provide further detail about the review process or its adjudication procedures.

7. Results Posted in the Registry

• Arm 1: Pembrolizumab/Vibostolimab Coformulation + Docetaxel vs Arm 3: Placebo + Docetaxel: hazard ratio 0.77 (95% CI 0.53–1.13), reported p = 0.091 (as reported in the registry).
• Arm 2: Pembrolizumab/Vibostolimab Coformulation vs Arm 3: Placebo + Docetaxel: hazard ratio 1.40 (95% CI 0.96–2.02), reported p = 0.962 (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 RECIST 1.1 by BICR 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:
  • Arm 1: Pembrolizumab/Vibostolimab Coformulation + Docetaxel: 29.9% (26/87) versus 15.3% (13/85) on control; risk difference 14.6 percentage points (95% CI 2.3 to 26.9), risk ratio 1.95 (1.08–3.54); unadjusted two-proportion z-test p = 0.022.
  • Arm 2: Pembrolizumab/Vibostolimab Coformulation: 6.0% (5/83) versus 15.3% (13/85) on control; risk difference -9.3 percentage points (95% CI -18.5 to -0.1), risk ratio 0.39 (0.15–1.06); unadjusted two-proportion z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm 1: Pembrolizumab/Vibostolimab Coformulation + Docetaxel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2: Pembrolizumab/Vibostolimab Coformulation and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival (OS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Arm 1: Pembrolizumab/Vibostolimab Coformulation + Docetaxel vs Arm 3: Placebo + Docetaxel: hazard ratio 0.76 (95% CI 0.50–1.15), reported p = 0.094 (as reported in the registry).
  • Arm 2: Pembrolizumab/Vibostolimab Coformulation vs Arm 3: Placebo + Docetaxel: hazard ratio 1.05 (95% CI 0.70–1.58), reported p = 0.597 (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 Arm 1: Pembrolizumab/Vibostolimab Coformulation + Docetaxel vs Arm 3: Placebo + Docetaxel 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 Arm 2: Pembrolizumab/Vibostolimab Coformulation vs Arm 3: Placebo + Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes extend the assessment beyond PFS. They include objective response rate and duration of response under RECIST 1.1 by blinded independent central review, overall survival, and adverse-event outcomes. The outcome types differ: response rate is a proportion, duration of response applies to response events, overall survival is time-to-event, and adverse-event measures describe harms and treatment discontinuation. These outcomes provide complementary information, but they do not answer the primary PFS question in the same way.

Across the secondary results, the response-rate estimates are numerically highest for the combination arm, while the coformulation-alone estimate is below the placebo-plus-docetaxel estimate. The overall-survival medians and hazard-ratio estimates do not provide a clear, precise separation between either experimental regimen and the comparator. This broad pattern is not a replacement for endpoint-specific interpretation, and secondary findings should not be treated as confirmation of the primary result.

Secondary analyses often involve multiple outcomes and comparisons. Testing many hypotheses increases the chance that at least one result appears notable by chance unless an appropriate multiplicity strategy is prespecified and applied. The registry record does not report whether the secondary analyses were adjusted for multiplicity, nor does it give a testing hierarchy. Any unadjusted p-values therefore carry less weight as confirmatory evidence than a result from a clearly specified, multiplicity-controlled analysis. Their estimates can still be informative descriptively, but the uncertainty and analysis context should remain visible.

Some endpoints may also depend on a subset of participants or events. For example, duration of response is conceptually relevant only after a response has occurred. The record does not give enough detail to describe all analysis populations or missing-data handling for each secondary outcome. Consequently, secondary outcomes can help characterize the breadth of the posted findings, but they cannot be combined into a single overall claim about efficacy or safety.

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

• Objective Response Rate (ORR) Per RECIST 1.1 by BICR Assessment
• Overall Survival (OS)
• Duration of Response (DOR) Per RECIST 1.1 by BICR Assessment
• Number of Participants Who Experienced an Adverse Event (AE)
• Number of Participants Who Discontinued Study Treatment Due to an AE

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure, so the analysis needs to account for both the timing of progression or death and the fact that some event times may not be observed during follow-up. The registry record states that the sponsor used regression with a Cox model for the reported hazard ratios. It does not report the full model specification, covariates, stratification factors, censoring rules, or diagnostic checks.

What does the hazard ratio summarize?

In general, a Cox-model hazard ratio compares the event hazard between groups over time. The event is progression or death, as defined for PFS. A hazard ratio is not a comparison of median survival times, and it should not be described as a direct percentage change in the probability of an event. The sponsor reported a hazard ratio of 0.77 for combination therapy versus placebo plus docetaxel, and 1.40 for coformulation alone versus placebo plus docetaxel. Each estimate is accompanied by a 95% confidence interval and a p-value. These are the sponsor's analyses, not newly calculated comparisons from the arm-level medians.

The Cox model conventionally relies on a proportional-hazards assumption: the relative hazard between groups is treated as stable over follow-up. That is a general description of the model, not confirmation that the assumption held in this trial. Assessment of that assumption is not reported in the registry record. When relative hazards change over time, one hazard ratio may be an incomplete summary, and survival curves or time-specific estimates may help describe the pattern. The registry record does not provide enough detail to assess this issue.

Why are the medians not the treatment comparison?

The arm-specific medians describe the estimated time-to-event distribution within each group. Their confidence intervals describe uncertainty around those estimates. Comparing medians informally does not reproduce the Cox model, because the model uses event-time information across follow-up rather than only the median point. The medians are useful descriptive summaries, while the reported hazard ratios are the sponsor's formal group comparisons. No difference between medians has been calculated for this explanation.

What does a confidence interval contribute?

A confidence interval gives a range of values compatible with the data under the statistical method and its assumptions. It reflects estimation uncertainty, rather than the range of individual participant outcomes. A wide interval indicates less precision than a narrow interval on the same scale. For the primary comparisons, both reported intervals include values on either side of the no-difference reference, so the estimates do not sharply distinguish a direction of effect. The intervals do not mean there is a 95% probability that the true effect is inside the particular interval; that is not the frequentist interpretation.

How should p-values be read?

A p-value describes how unusual data at least as discordant with a specified null hypothesis would be, assuming that hypothesis and the analysis model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary p-values are 0.091 and 0.962. In the absence of a reported multiplicity procedure, they should be interpreted as the values attached to the sponsor's individual comparisons, not as evidence that all testing across outcomes and hypotheses was controlled at a specified overall error rate.

What does blinded independent review add?

Blinded independent central review means the primary progression assessment was made by reviewers described as independent and blinded to treatment assignment. In general, this can limit assessment bias when progression is based on imaging criteria. It does not eliminate other sources of bias, ensure that every assessment is complete, or replace the need to understand missing scans and censoring. Details of review logistics, disagreement resolution and missing assessment handling are not reported in the registry record.

The posted primary analyses use all randomized participants as the stated population for the outcome. This is useful because maintaining randomized groups can preserve comparability created by random assignment. However, the record does not state how participants with missing outcome information were handled, whether any participants were excluded from the analysis, or the exact analysis population definition for each comparison beyond the stated all-randomized population for PFS. Those details matter because incomplete follow-up can affect time-to-event estimates if censoring is related to prognosis or treatment experience.

Other results use different methods because the outcomes differ. Objective response rate is a binary outcome, while overall survival is also time-to-event. The registry record reports a Miettinen & Nurminen method for the response-rate comparisons and Cox regression for overall-survival hazard ratios. General methods should be matched to the outcome type: binary methods compare response proportions, whereas time-to-event methods retain information about event timing and follow-up. Their estimates and p-values are not interchangeable across endpoints.

Finally, the registry record does not report the statistical analysis plan, prespecified model details, interim analyses, or the rationale for the selected enrollment. Without those elements, readers cannot determine from the posted record whether every analysis was prespecified, how all outcome testing was organized, or what alternative analyses were considered. The sponsor-reported analyses remain the primary source for the trial's formal comparison; any simpler re-calculation should be treated as a descriptive check rather than a replacement.

11. Confidence Intervals and Precision

The PFS median estimates have 95% confidence intervals of 3.9 to 6.8 months for pembrolizumab/vibostolimab plus docetaxel, 1.8 to 4.0 months for coformulation alone, and 2.8 to 5.7 months for placebo plus docetaxel. The intervals overlap, but overlap between arm-specific intervals is not itself a formal test of a treatment difference. The sponsor's Cox-model comparison is the relevant reported analysis for the primary endpoint.

For the hazard ratio of 0.77, the interval runs from 0.53 to 1.13; for the hazard ratio of 1.40, it runs from 0.96 to 2.02. Both intervals cover values on either side of the no-difference reference. That means the posted estimates retain uncertainty about direction as well as magnitude. The first comparison is compatible with a lower event hazard and also with values indicating a higher event hazard; the second likewise does not exclude either direction. The width of each interval matters: the point estimate alone gives a more definite impression than the uncertainty supports.

Confidence intervals describe precision conditional on the analysis and its assumptions. They do not measure the chance that an individual participant will have a particular outcome, nor do they establish the clinical importance of an estimate. The record does not provide a prespecified threshold for a clinically important PFS difference, so clinical importance cannot be judged from statistical significance alone. Follow-up is described as up to approximately 21 months; the registry record does not provide additional detail about follow-up distribution or the number at risk over time.

As a general principle, greater precision is usually reflected by narrower intervals, while limited event information or variability can leave estimates less precise. The confidence intervals should therefore be read together with the hazard-ratio point estimates, the p-values, the model, and the trial's design. They do not turn an uncertain result into evidence of no possible effect.

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 are based on the observed effect, not on the trial's original design assumptions. The registry record does not report the original sample-size justification. For time-to-event outcomes, the figures are total events required; for other outcomes, they are participants per arm. Thus the PFS and overall-survival planning illustrations refer to total events, while the response-rate illustrations refer to participants per arm.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is expressed as a stated fraction of the observed effect: 100%, 75% or 50%. The figures do not describe the observed enrollment or the number of events that occurred in this trial. They are planning illustrations under the listed assumptions.

The 80% power column gives the number of participants per arm, or total events for a time-to-event outcome, that the illustration estimates would be needed to have an 80% chance of detecting the assumed effect under the stated model and significance level. The 90% power column expresses the corresponding requirement for a 90% chance. Power is a property of a planned study under specified assumptions; it is not the probability that a reported finding is true.

Smaller target effects generally require more information to detect reliably. In the illustrations, planning for 75% or 50% of the observed effect requires more participants or events than planning for the full observed effect. This is not observed power. The illustrations should not be read as a retrospective verdict on whether the completed study was adequately powered, because they rely on the observed effect and assumptions that may not match the trial's original planning.

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 = 0.770, so ln(HR) = -0.2614.
2. d = 4 × (1.96 + 0.842)² / [ln(0.770)]² = 459.6, rounded up to 460 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 <- 0.77                              # 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(4725188)
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 = 460 (80% power), 616 (90% power)
 75% of observed effect: events = 818 (80% power), 1,094 (90% power)
 50% of observed effect: events = 1,839 (80% power), 2,462 (90% power)
Simulated power with 460 events: 0.787 (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 656 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 255 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 <- 3.2          # control-arm median, months (converted from the posted unit)
hr          <- 0.77          # 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: 344         p (1-sided)   0.0001
 Events: 208        ~HR at bound   0.5973
   Month: 13    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.77   0.0338
   IA 2: 67%                   Z   2.5114
      N: 572         p (1-sided)   0.0060
 Events: 415        ~HR at bound   0.7814
   Month: 21    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.77   0.5603
       Final                   Z   1.9930
      N: 656         p (1-sided)   0.0231
 Events: 623        ~HR at bound   0.8523
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.77   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 reported hazard ratios, confidence intervals and p-values are the sponsor's Cox-regression analyses. The primary outcome type is time-to-event, and the record's statistical description specifies that only sponsor-reported hazard ratios are used for the comparisons. The arm-specific medians and their confidence intervals are descriptive summaries, not independent substitutes for those model-based tests.

The posted sponsor analysis reports a hazard ratio of 0.77 (95% CI 0.53 to 1.13; p = 0.091) for pembrolizumab/vibostolimab plus docetaxel versus placebo plus docetaxel. For coformulation alone versus placebo plus docetaxel, it reports a hazard ratio of 1.40 (95% CI 0.96 to 2.02; p = 0.962). These are the primary comparative estimates to use when describing the registry's PFS findings. The registry record does not report enough model detail to reproduce the Cox analyses from the arm-level median summaries.

For the response-rate endpoint, the sponsor reports comparisons using the Miettinen & Nurminen method, whereas simple unadjusted recalculations use different summaries and methods. Those results need not match exactly because they are not identical analyses. The record does not identify a discrepancy flag requiring the recalculated result to replace or supersede the sponsor's analysis. In general, when a recalculation and the sponsor's stated method differ, the distinction should be made explicit: the sponsor's own analysis is the formal posted result, and a simple recalculation is a descriptive check, not a replacement.

The registry record does not report a complete statistical analysis plan or enough information to independently verify all sponsor model choices. Interpretation should accordingly preserve the distinction between reported sponsor analyses and derived descriptive calculations.

16. Multiplicity, Missing Data and Analysis Populations

The registry record describes dual primary hypotheses: pembrolizumab/vibostolimab plus docetaxel and pembrolizumab/vibostolimab alone are each compared with placebo plus docetaxel for PFS. It does not report how the type I error was allocated across those two primary comparisons, whether a testing hierarchy was used, or whether a multiplicity adjustment was applied. This matters because separate hypothesis tests can increase the chance of a false-positive result when considered together. The reported p-values should therefore be understood as the values for the individual sponsor analyses; the record does not establish an overall error-control procedure.

The record also lists several secondary outcomes, but does not report whether their analyses were confirmatory, how they were ordered, or whether their p-values were adjusted for multiple testing. Without this information, secondary p-values should be treated cautiously and not interpreted as if they were part of a single prespecified, protected testing sequence.

Missing-data handling is not reported in the registry record. For PFS, important details would include censoring rules, treatment of missing or unevaluable scans, and how follow-up ending before progression or death was handled. The record identifies the PFS population as all randomized participants, but does not explain whether any participants lacked evaluable outcome data or how those cases entered the model. The exact analysis populations for secondary outcomes are also not fully described in the posted information.

Interim analyses are not reported in the registry record. The detailed statistical analysis plan, including covariate adjustment, stratification, sensitivity analyses and protocol-defined estimands, is also not reported. These omissions limit assessment of whether the analyses followed prespecified procedures and how robust the results are to alternative assumptions. They do not invalidate the posted estimates, but they narrow the conclusions that can be drawn from the registry record alone.

As a general matter, missing outcomes and multiplicity are distinct issues. Missing-data methods address incomplete observation; multiplicity methods address the interpretation of repeated statistical tests. A sound interpretation requires attention to both, and the available record does not supply all relevant details.

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: pneumonia (12.0%), febrile neutropenia (3.6%), anaemia (3.5%), diarrhoea (3.5%), covid-19 (3.5%).

The safety entries report serious adverse events among 48 of 85 participants in the combination arm, 26 of 83 in the coformulation-alone arm, and 37 of 83 in the placebo-plus-docetaxel arm. These counts are presented alongside the numbers at risk for the serious-adverse-event summaries. The registry record also lists pneumonia at 12.0% as a serious adverse-event term, followed by febrile neutropenia at 3.6%, anaemia at 3.5%, diarrhoea at 3.5%, COVID-19 at 3.5%, and septic shock at 3.5%.

These figures describe reported events in the registry record. They do not establish that a treatment caused a particular event, and the counts alone do not describe event severity beyond the serious classification, duration, recurrence, or timing. The record separately reports other adverse events and treatment discontinuations due to adverse events, but the available summary does not provide a complete clinical narrative for those outcomes. Safety comparisons also require attention to exposure and follow-up; detailed exposure-adjusted analyses are not reported in the registry record.

Because the arms differ in assigned treatment, event counts should be read in the context of the regimen and reported population. They are not a substitute for a full safety analysis, and they do not support individual medical decisions.

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

The primary findings are estimates of PFS for the randomized groups in this phase 2 study, together with sponsor-reported hazard-ratio comparisons. The combination arm's hazard-ratio point estimate was below the no-difference reference, while its confidence interval extended across that reference and its p-value was 0.091. The coformulation-alone hazard-ratio estimate was above the reference, with a confidence interval that also crossed it and p = 0.962. The posted primary analyses therefore do not provide clear statistical evidence of a difference under the conventional 0.05 threshold.

This does not establish that the regimens have identical effects, nor does it exclude effects that could matter. The confidence intervals retain uncertainty about both direction and magnitude, and the registry record does not state a threshold for clinical importance. A non-significant result is not proof of no effect. Conversely, a point estimate that favors one direction is not by itself proof that the regimen caused a benefit.

The study included a placebo-plus-docetaxel control, so the combination comparison evaluates the coformulation added to docetaxel, whereas the monotherapy comparison is against placebo plus docetaxel. The trial does not report a direct randomized comparison between the two active regimens. Its findings should not be used to rank those regimens against one another based only on the posted summaries.

The secondary outcomes and safety results add context but do not settle the primary question. Multiple outcomes, missing-data details and multiplicity procedures are not fully described in the registry record. The findings apply to the enrolled study population and the recorded follow-up, and cannot be assumed to generalize to other settings or patient groups. Overall, the record supports a careful description of the estimates and their uncertainty, not a definitive claim that a treatment works or does not work.

19. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its estimand, model and uncertainty rather than through a single arm-level number. PFS is a time-to-event outcome that combines progression and death, and the sponsor's Cox-model hazard ratios use more event-time information than the medians alone. The median summaries make the distribution easier to describe, but they do not replace the modeled comparisons.

The study also has two primary comparisons against a shared control. That structure makes the multiplicity plan important: interpretation of each p-value depends partly on how the hypotheses were organized and whether error control was applied across them. The registry record does not report those details. This is a useful reminder that a list of primary hypotheses is not, by itself, a complete account of the inferential plan.

Finally, statistical precision matters as much as direction. Both primary hazard-ratio intervals include the no-difference reference, and the p-values do not cross the conventional 0.05 threshold. Those features should be described without converting uncertainty into a claim of equivalence or a claim of benefit. The planning illustrations also demonstrate how study requirements depend on the effect size one aims to detect and on assumptions about allocation and significance level; they are not retrospective evidence of the study's power.

The trial is therefore informative as a case study in interpreting randomized, multi-arm evidence: separate descriptive summaries from formal comparisons, distinguish sponsor analyses from simpler checks, and keep multiplicity, missingness and precision in view.

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 does not report a full statistical analysis plan, including detailed Cox-model specification, covariates, stratification, proportional-hazards assessment, censoring rules or sensitivity analyses. Those omissions limit independent evaluation of the primary model and the robustness of the reported hazard ratios. The record also does not report the original sample-size justification, so the enrollment cannot be assessed against the sponsor's planned assumptions using this record alone.

There are two primary comparisons against the same control group, but the multiplicity procedure is not reported. The plan for handling multiple secondary outcomes is also not reported. This makes it difficult to determine whether the reported p-values represent individual tests or are interpreted within a controlled testing strategy. Interim analyses are not reported.

Although all randomized participants are identified as the primary PFS population, the registry record does not explain missing scan handling, censoring, protocol deviations or the exact analysis populations for all outcomes. The stated follow-up timeframe is up to approximately 21 months, but detail on follow-up completeness and event accumulation is not reported. The arm-level entries for outcomes may also reflect different available information, and the record does not give enough detail to assess this fully.

The results come from a phase 2 study in participants with metastatic non-small cell lung cancer whose disease progressed after specified prior treatment. The findings should not automatically be generalized to people outside that setting. The posted record also does not provide enough detail to assess site-level variation, adherence, treatment exposure differences, or the consequences of treatment discontinuation. These are limits on interpretation, not evidence that the results are invalid.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Pembrolizumab/Vibostolimab Coformulation (MK-7684A) or Pembrolizumab/Vibostolimab Coformulation Plus Docetaxel Versus Docetaxel for Metastatic Non Small Cell Lung Cancer (NSCLC) With Progressive Disease After Platinum Doublet Chemotherapy and Immunotherapy (MK-7684A-002, KEYVIBE-002) — NCT04725188.
• Registry record last updated 2025-08-15; status last verified 2025-07.
• Results first posted 2024-04-02.
• 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

KEYVIBE-002 (NCT04725188) was a completed, randomized, double-blind, parallel-group phase 2 study in metastatic non-small cell lung cancer after progression following platinum doublet chemotherapy and prior immunotherapy. The study enrolled 255 participants and compared pembrolizumab/vibostolimab coformulation plus docetaxel, coformulation alone, and placebo plus docetaxel.

The primary outcome was PFS by RECIST 1.1, assessed by blinded independent central review. The sponsor-reported Cox analyses gave hazard ratios of 0.77 (95% CI 0.53 to 1.13; p = 0.091) for combination therapy versus placebo plus docetaxel, and 1.40 (95% CI 0.96 to 2.02; p = 0.962) for coformulation alone versus placebo plus docetaxel. Both intervals include values on either side of the no-difference reference.

The registry record does not report the original sample-size justification, full multiplicity strategy, detailed missing-data methods or interim analyses. Those limits should accompany interpretation of the posted results.