Study of Pemetrexed+Platinum Chemotherapy With or Without Pembrolizumab (MK-3475) in Participants With First Line Metastatic Nonsquamous Non-small Cell Lung Cancer (MK-3475-189/KEYNOTE-189)-Japan Extension Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Pemetrexed+Platinum Chemotherapy With or Without Pembrolizumab (MK-3475) in Participants With First Line Metastatic Nonsquamous Non-small Cell Lung Cancer (MK-3475-189/KEYNOTE-189)-Japan Extension Study (NCT03950674), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS) Per Response Evaluation Criteria in Solid Tumors (RECIST) 1.1 as Assessed by Blinded Central Imaging.

2. Clinical Question

The trial was a Japan extension of global study MK-3475-189. Its question concerns a treatment strategy in a defined setting: first-line therapy for advanced or metastatic nonsquamous disease, with platinum choice left to the investigator. The primary endpoint counted progression or death, rather than tumor response alone, and was assessed by blinded central imaging.

The comparison is randomized and parallel, with pembrolizumab or placebo added to a chemotherapy backbone. That design aims to make the groups comparable at assignment and to isolate the contrast between the pembrolizumab-containing strategy and its placebo counterpart. The posted results describe a hazard ratio for progression-free survival, which compares event rates over follow-up, alongside group medians. These measures answer related but distinct questions: the medians describe the middle of each group’s event-time distribution, while the hazard ratio summarizes the relative event hazard over time under the analysis model.

3. Trial Design

The registry describes a completed, randomized, phase III, parallel-group study with triple masking. Enrollment was 40. The study started on 2016-02-22, and primary completion was recorded as 2019-05-20. Its title identifies the work as the Japan extension of KEYNOTE-189; the brief summary likewise describes it as an extension of the global study. The registry lists the sponsor as Merck Sharp & Dohme LLC.

The two main groups received the same pemetrexed-and-platinum chemotherapy backbone, with pembrolizumab in one group and saline placebo in the other. The platinum agent could be cisplatin or carboplatin at the investigator’s choice. The described schedules use treatment every three weeks, with the initial chemotherapy combination followed by continued pembrolizumab or placebo with pemetrexed. The arm descriptions also list vitamin supplementation and other supportive or treatment-related agents.

The progression-free survival analysis included all randomized participants. The arm-level outcome records 25 participants in the pembrolizumab group and 15 in the placebo group. Those arm counts reflect the posted analysis, not an equal allocation. The registry record does not report the original trial’s sample-size justification or the assumptions used to plan enrollment.

The primary outcome timeframe is up to approximately 31 months. With Amendment 11, effective date 31-Jan-2022, participants were to be discontinued from this study and enrolled in an extension study once the objectives had been met or the study had ended, so protocol-defined assessments and treatment could continue. That note describes the registry’s follow-on arrangements; it does not change the definition of the posted primary endpoint.

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: Four participants randomized to placebo treatment had switched over to receive pembrolizumab monotherapy. Participants receiving pembrolizumab in the first course and those who switched over from placebo to pembrolizumab were eligible to receive a second course of pembrolizumab if they met certain criteria. Data from the second course treatment contributed to safety data only. Final analyses for all primary and secondary outcome measures were done at the protocol-specified cutoff (20-May-2019).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population consisted of 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.

Population: The Baseline Analysis Population consisted of all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS) Per Response Evaluation Criteria in Solid Tumors (RECIST) 1.1 as Assessed by Blinded Central Imaging, measured over Up to approximately 31 months.

Progression-free survival (PFS) measures the time from randomization until the first documented progressive disease or death from any cause, whichever occurs first. The registry defines progression using RECIST 1.1: a specified increase in the sum of target-lesion diameters relative to the smallest sum recorded on study, together with an absolute increase; the appearance of new lesions also counts as progression. The assessment was by blinded central imaging.

PFS is used in cancer trials because it captures the time until disease progression or death, combining radiographic progression and death into a time-to-event outcome. It differs from overall survival, which concerns death, and from response rate, which describes whether a response was recorded. A participant who has not had the event by the end of observed follow-up may contribute information up to the last relevant assessment rather than being treated as though progression occurred at that time. This is the general time-to-event approach; the registry record does not detail the censoring rules used for this analysis.

The posted group medians are 16.5 months for pembrolizumab with chemotherapy and 7.1 months for placebo with chemotherapy. The reported comparison is a hazard ratio, which describes the relative event hazard over the observed follow-up under the analysis. A median contrast and a hazard ratio summarize different features of the event-time distributions, so neither should be treated as a complete description of the other.

7. Results Posted in the Registry

• Pembrolizumab With Pemetrexed and Platinum Chemotherapy Followed by Pembrolizumab and Pemetrexed vs Placebo With Pemetrexed and Platinum Chemotherapy Followed by Placebo and Pemetrexed: hazard ratio 0.62 (95% CI 0.27–1.42), reported p = 0.125 (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 Response Rate (ORR) Per RECIST 1.1 as Assessed by Blinded Central Imaging

• 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:
  • Pembrolizumab With Pemetrexed and Platinum Chemotherapy Followed by Pembrolizumab and Pemetrexed: 56.0% (14/25) versus 33.3% (5/15) on control; risk difference 22.7 percentage points (95% CI -8.1 to 53.5), risk ratio 1.68 (0.76–3.72); unadjusted two-proportion z-test p = 0.165.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pembrolizumab With Pemetrexed and Platinum Chemotherapy Followed by Pembrolizumab and Pemetrexed and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes listed in the registry span response, duration of response and safety. The posted ORR estimates point in the same broad direction as the PFS point estimate: the observed response percentage is higher in the pembrolizumab group. The response comparison remains imprecise, and it does not independently settle the uncertainty in the primary time-to-event result.

Duration of response and adverse-event outcomes are also named as secondary outcomes, but numerical results for every listed secondary endpoint are not reported in the registry record in the information analyzed. The available secondary evidence therefore does not form a complete, consistently quantified picture across all listed outcomes. Safety counts are discussed separately because they describe harms rather than efficacy.

Secondary findings generally carry less inferential weight than the designated primary outcome, especially when many outcomes are examined. Testing multiple outcomes increases the chance that some appear noteworthy by chance alone unless the analysis accounts for multiplicity. The registry record does not report whether a multiplicity adjustment or a hierarchical testing strategy was used. The unadjusted ORR recalculation should consequently be read as descriptive support for the observed pattern, not as a confirmatory finding.

Results across different endpoints should not be combined informally into a single verdict. Response status and PFS are related but not identical: a response is a tumor-measurement outcome, while PFS incorporates time to progression or death. Nor should secondary efficacy observations be treated as substitutes for an unavailable numerical result on another endpoint. The appropriate overall reading is that the available response estimate is directionally consistent with the primary point estimate, while uncertainty and incomplete reporting of other secondary results limit the strength of cross-endpoint conclusions.

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

• Overall Response Rate (ORR) Per RECIST 1.1 as Assessed by Blinded Central Imaging
• Duration of Response (DOR) Per RECIST 1.1 as Assessed by Blinded Central Imaging
• Number of Participants Who Experienced an Adverse Event (AE)
• Number of Participants Who Discontinued Any Study Drug Due to an AE

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time-to-event data. Such data record not only whether an event occurred but also the time until it occurred. In PFS, the event is documented progression or death, whichever comes first. Participants whose event time is not observed during follow-up can have incomplete event-time information. Standard time-to-event methods can retain their available follow-up through censoring, but the registry record does not report the censoring rules or detailed handling of incomplete assessments.

What does the median PFS describe?

A median event time marks the point at which the estimated event-time distribution reaches its midpoint. The posted medians are 16.5 months for the pembrolizumab group and 7.1 months for the placebo group. A median is useful because it expresses the endpoint in familiar time units. It does not convey the full shape of the survival curve, the pattern of events over time, or the uncertainty for each individual. The registry gives a 95% confidence interval for each median, and those intervals are wide.

What does the hazard ratio describe?

The hazard ratio compares the event hazards between the randomized groups over follow-up. The reported value is 0.62, for pembrolizumab with chemotherapy relative to placebo with chemotherapy. A value below the no-difference reference points toward a lower event hazard in the first group; it is not a percentage change in the median and should not be interpreted as an absolute risk difference. A hazard ratio is most straightforward to interpret when the relative hazards are reasonably stable over time. Whether that assumption was assessed, or whether alternative time-varying effects were considered, is not reported in the registry record.

How should the log-rank result be read?

The registry reports a log-rank method, a 95% confidence interval of 0.27 to 1.42 for the hazard ratio, and p = 0.125. The log-rank test compares event-time experience across groups while accounting for follow-up time and censoring under its assumptions. The interval expresses uncertainty around the estimated relative effect. Because it includes the no-difference value, the data do not precisely distinguish a lower hazard from no difference or a higher hazard. The p-value is a test summary, not an effect-size measure. The registry record does not report additional details of the model or diagnostics.

Why can the interval be broad?

Precision in time-to-event analysis depends particularly on the amount and timing of event information, not only on the number randomized. A small extension study can yield relatively few events for estimating a group contrast, and uneven group sizes can also limit precision. The posted enrollment and arm counts are modest, but the total event count used in the primary analysis is not reported in the registry record. The confidence interval is the direct evidence of uncertainty; it should not be replaced by a claim about power.

General statistical context: censoring is not equivalent to observing that a participant remained event-free indefinitely. A censored participant contributes information up to the time their event status was last known, subject to the method’s assumptions. If censoring differs meaningfully between groups or is related to prognosis in a way the analysis does not accommodate, estimates may be affected. The registry does not report enough detail to assess those conditions for this result.

The secondary ORR outcome is binary: participants are classified according to whether response criteria were met. Its group estimates are percentages with confidence intervals, and the re-calculated comparison is an unadjusted risk difference. That measure expresses the difference in observed response proportions, not a time-to-response contrast or a hazard ratio. The registry reports no sponsor analysis for that secondary comparison. The listed planning illustrations for ORR are based on the observed effect and specified assumptions, not on a reported original design calculation.

These methods answer different questions. PFS considers timing of progression or death; ORR considers whether a response occurred; adverse-event counts describe safety observations. A result on one endpoint cannot be substituted for another. The registry record lists additional secondary outcomes but does not provide numerical results for all of them in the registry record analyzed. It also does not report a detailed statistical analysis plan, interim analyses, missing-data procedures, or multiplicity strategy.

11. Confidence Intervals and Precision

Confidence intervals communicate the range of effect estimates reasonably compatible with the observed data under the analysis and its assumptions. They are not guarantees that the true effect lies inside a particular interval, and they do not describe the spread of individual participant outcomes. Their width is a practical indicator of how much uncertainty remains.

For the primary comparison, the hazard ratio is 0.62 and its 95% confidence interval extends from 0.27 to 1.42. The interval includes the no-difference value and allows both a lower and a higher hazard in the pembrolizumab group. Thus, the point estimate alone gives a more favorable impression than the full interval warrants. The confidence interval is broad enough that the magnitude and direction of the underlying effect are not pinned down precisely by this study.

The median PFS intervals are also broad: 8.8 to 21.1 months for the pembrolizumab group and 4.7 to 21.4 months for the placebo group. Overlap between group-specific intervals is not itself a test of the treatment contrast. The reported hazard ratio and its interval are the registry’s direct comparative summary for PFS.

The ORR confidence intervals are broad as well: 34.9% to 75.6% for the pembrolizumab group and 11.8% to 61.6% for the placebo group. They indicate substantial uncertainty in each response estimate. The risk-difference interval extends from -0.081 to 0.534, which also includes no difference. Together, the intervals caution against treating the observed point estimates as precise effects. The modest size of this extension study and the arm counts of 25 and 15 provide context for that uncertainty, but the interval is the key expression of precision.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations use the observed effect as a starting point and show hypothetical requirements for detecting the full observed effect, 75% of that effect, or 50% of that effect. For the PFS comparison, the figures are total events, not participants per arm. For the ORR comparison, the figures are participants per arm. These are planning quantities for hypothetical studies, not descriptions of the number enrolled in this trial.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect equal to the stated fraction of the observed effect. For time-to-event planning, the total event figures use the Schoenfeld approach. The original design assumptions for this Japan extension study, including its sample-size justification, are not reported in the registry record.

The 80% power column gives the modeled number of events or participants needed for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is real. The 90% power column expresses the corresponding planning target for a higher chance of detection. Neither column tells whether this completed study had a particular probability of finding a result, and neither is an observed power estimate.

Smaller effects are harder to distinguish from random variation, so the planning figures rise when the assumed effect is reduced from the full observed effect to 75% or 50%. The figures depend on the observed effect, which is uncertain, and should be treated as illustrations rather than definitive design recommendations. They do not account for unreported features of the original trial design.

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 = 0.620, so ln(HR) = -0.4780.
2. d = 4 × (1.96 + 0.842)² / [ln(0.620)]² = 137.4, rounded up to 138 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 <- 0.62                              # 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(3950674)
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 = 138 (80% power), 184 (90% power)
 75% of observed effect: events = 245 (80% power), 327 (90% power)
 50% of observed effect: events = 550 (80% power), 736 (90% power)
Simulated power with 138 events: 0.796 (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 215 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 40 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          <- 0.62          # 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: 148         p (1-sided)   0.0001
  Events: 62        ~HR at bound   0.3886
   Month: 17    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.62   0.0338
   IA 2: 67%                   Z   2.5114
      N: 216         p (1-sided)   0.0060
 Events: 124        ~HR at bound   0.6361
   Month: 26    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.62   0.5603
       Final                   Z   1.9930
      N: 216         p (1-sided)   0.0231
 Events: 185        ~HR at bound   0.7460
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.62   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 registry reports the sponsor’s PFS comparison as a log-rank hazard ratio of 0.62, with a 95% confidence interval of 0.27 to 1.42 and p = 0.125. The comparison corresponds to pembrolizumab with chemotherapy versus placebo with chemotherapy. The recalculated primary comparison uses that reported hazard ratio; the registry record does not flag a discrepancy between the posted comparison and the reported analysis.

A simple recalculation from group-level summaries cannot reconstruct a time-to-event analysis. The hazard ratio and log-rank result depend on event times and censoring patterns, information that is not represented by the two medians and their confidence intervals alone. For that reason, the sponsor’s reported analysis is the relevant comparative analysis for PFS, rather than an independently derived test from summary statistics.

The sponsor-reported result should still be interpreted with its uncertainty. The confidence interval includes the no-difference value, and the p-value is 0.125. These features mean that the estimate is not precise enough to establish a clear separation between groups in this extension study. The reported analysis is the primary source for the comparative PFS statistic; it does not remove the limitations associated with the study’s size or the width of the interval.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, comparisons or analysis opportunities. Without an appropriate strategy, the chance of at least one apparently positive result can increase as the number of tests grows. The registry lists seven outcome measures and reports two analyses in the information summarized for this study. The primary hypothesis refers to both PFS and overall survival, while the posted primary outcome analyzed is PFS and the listed secondary outcomes include response, duration of response and adverse events.

The registry record does not report whether multiplicity was controlled, how the primary hypotheses were ordered, or whether any secondary analyses were formally confirmatory. It also does not report interim analyses or stopping rules. Therefore, the reported p-value should be interpreted as the result of the stated log-rank analysis, without assuming a particular adjustment or testing hierarchy. Secondary unadjusted results should be treated cautiously in the presence of multiple outcomes.

The primary analysis population is described as all randomized participants, which is a relevant design feature because retaining participants according to randomized group can preserve the benefits of randomization. The record does not report further details on exclusions, protocol deviations, missing imaging, censoring, or how participants with incomplete outcome assessments were handled. Those omissions prevent an independent assessment of the exact analysis population and missing-data procedures beyond the statement that the primary population consisted of all randomized participants.

Missing outcome information can affect estimates if it is related to prognosis or differs between groups. In time-to-event analysis, censoring permits use of partial follow-up, but valid interpretation depends on assumptions about how censoring relates to event risk. The registry does not provide the information needed to evaluate those assumptions. These are reporting limitations, not evidence that any particular analysis procedure was or was not used.

The registry also does not report the original sample-size justification, detailed statistical analysis plan, or all planned-versus-reported analysis decisions. The separate planning illustrations are based on the observed effect and stated modeling assumptions; they are not evidence of the trial’s original design rationale.

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: pneumonitis (25.0%), interstitial lung disease (13.3%), pyrexia (8.0%), diarrhoea (6.7%), tumour necrosis (6.7%).

The safety records list serious adverse events among 9 of 25 participants in the pembrolizumab-with-chemotherapy group and 6 of 15 participants in the placebo-with-chemotherapy group. These counts describe the participants recorded as affected in each group; they do not establish that treatment caused an event. The groups are small, and the counts should be read descriptively rather than as a precise comparison of risk.

The registry also lists other adverse events for all 25 participants in the pembrolizumab group and all 15 participants in the placebo group. Separate safety records include participants who switched over to pembrolizumab monotherapy and second-course treatment groups. Those are distinct registry categories and should not be added to the main randomized groups or interpreted as a direct randomized comparison.

The serious-event terms listed most prominently include pneumonitis, interstitial lung disease, pyrexia, diarrhoea, tumour necrosis and cerebral haemorrhage, with percentages recorded in the registry. The registry record does not provide enough detail in these data to establish causal attribution or compare each term reliably between randomized groups. Death counts are also recorded in the safety data, but they are not a substitute for the defined PFS analysis.

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

The posted PFS results show a longer observed median in the pembrolizumab-plus-chemotherapy group than in the placebo-plus-chemotherapy group, alongside a hazard-ratio point estimate favoring the pembrolizumab group. These are estimates from the randomized comparison in this Japan extension study. The confidence interval is broad and includes the no-difference value, so the result does not precisely establish the magnitude or direction of the underlying comparative effect.

The reported p-value does not prove that there is no effect, just as the point estimate does not prove that there is a benefit. Statistical uncertainty applies in both directions. The data are compatible with a range of effects, and the study’s limited size is one reason not to overinterpret a single estimate. The result is neither a statement about what happened to every participant nor a guarantee about future outcomes.

The ORR point estimates are directionally consistent with the PFS point estimate, but their intervals are wide, and the unadjusted comparison is not a substitute for the primary analysis. Other secondary endpoint results are not fully reported in the registry information analyzed. Safety counts provide a descriptive account of recorded adverse events and should not be read as proof of causation or as a complete characterization of comparative safety.

This result does not establish that one treatment strategy works or does not work in all patients, settings or populations. It concerns adults in Japan with the specified advanced or metastatic nonsquamous disease who had not previously received systemic therapy for advanced disease, under the regimens described in the registry. The follow-on extension arrangement and limited follow-up timeframe also define the context of the posted record. Statistical interpretation should remain tied to that population, endpoint, analysis and uncertainty.

19. Why This Trial Matters Statistically

This study illustrates why an estimated treatment effect should be read together with its uncertainty. The median PFS values and the hazard-ratio point estimate point in a favorable direction for the pembrolizumab-containing group, but the hazard-ratio interval is wide and includes the no-difference value. A reader who focuses only on the point estimate or the difference between medians would miss how much uncertainty remains.

It also demonstrates that a randomized comparison can still be imprecise. Randomization addresses comparability at assignment in expectation; it does not ensure that a small study will produce a narrow confidence interval or a definitive result. In time-to-event studies, the amount of event information and the follow-up pattern matter, and the registry does not report the total events used for the primary analysis.

The separation between a primary outcome and secondary outcomes matters as well. PFS, response and adverse events describe different aspects of treatment experience. A directionally similar secondary estimate can add context, but it cannot erase uncertainty in the primary result, particularly when multiplicity procedures are not reported. Finally, the planning illustrations show how assumptions about the effect to be detected affect hypothetical resource requirements; they should not be mistaken for the study’s original design calculation or an assessment of its observed power.

20. Limitations

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

This is a small Japan extension study, with 40 enrolled and arm counts of 25 and 15 in the primary outcome record. The confidence interval for the reported hazard ratio is broad, limiting precision. The total number of PFS events and detailed follow-up distribution are not reported in the registry record, making it difficult to assess how much event information supported the comparison.

The primary outcome timeframe is up to approximately 31 months. The registry describes a later extension arrangement in which participants could continue protocol-defined assessments and treatment in an extension study, but the information analyzed does not provide further outcome follow-up from that arrangement. The posted PFS result should therefore be interpreted within its stated analysis timeframe.

The registry record does not report the original sample-size rationale, full statistical analysis plan, missing-data procedures, censoring details, multiplicity strategy or interim analyses. It also does not provide numerical results for every listed secondary endpoint. These gaps restrict assessment of analysis choices and the broader pattern across outcomes. They should be understood as limits of the registry information, not as evidence that a particular procedure was omitted.

The primary endpoint relies on RECIST 1.1 progression assessed by blinded central imaging. This is a defined and structured outcome, but the registry summary does not give detailed information on imaging schedules, adjudication procedures or assessment availability. The hazard ratio also depends on time-to-event assumptions; diagnostics for those assumptions are not reported. Finally, the arm sizes are unequal, and the study’s extension setting means these results should not be generalized automatically beyond the population and treatment context described.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Pemetrexed+Platinum Chemotherapy With or Without Pembrolizumab (MK-3475) in Participants With First Line Metastatic Nonsquamous Non-small Cell Lung Cancer (MK-3475-189/KEYNOTE-189)-Japan Extension Study — NCT03950674.
• Registry record last updated 2024-06-10; status last verified 2024-05.
• Results first posted 2020-06-11.
• 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, phase III, triple-masked Japan extension study comparing pembrolizumab plus pemetrexed and platinum chemotherapy with placebo plus pemetrexed and platinum chemotherapy in first-line advanced or metastatic nonsquamous non-small cell lung cancer. The primary outcome was PFS assessed by blinded central imaging and defined as time to progression or death.

The posted medians were 16.5 months and 7.1 months, respectively. The reported hazard ratio was 0.62, with a 95% confidence interval of 0.27 to 1.42 and p = 0.125. The point estimate favors the pembrolizumab group, but the interval is broad and includes no difference. The ORR estimates are directionally consistent but imprecise. The small extension-study sample, unreported analysis details and incomplete numerical reporting for some secondary outcomes limit further inference.