A Study of Atezolizumab in Combination With Carboplatin or Cisplatin + Pemetrexed Compared With Carboplatin or Cisplatin + Pemetrexed in Participants Who Are Chemotherapy-Naive and Have Stage IV Non-Squamous Non-Small Cell Lung Cancer (NSCLC) (IMpower 132): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Atezolizumab in Combination With Carboplatin or Cisplatin + Pemetrexed Compared With Carboplatin or Cisplatin + Pemetrexed in Participants Who Are Chemotherapy-Naive and Have Stage IV Non-Squamous Non-Small Cell Lung Cancer (NSCLC) (IMpower 132) (NCT02657434), a randomized phase 3 study. The primary outcome is Progression Free Survival (PFS) as Assessed by the Investigator Using Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST v1.1).

2. Clinical Question

3. Trial Design

This was a Phase III, randomized, open-label, parallel-group study. The registry record describes it as multicenter and reports a planned 1:1 allocation to two treatment groups. The study is listed as completed, with enrollment of 578. The recorded start date is 2016-04-30 and the primary completion date is 2019-07-18.

Arm A combined atezolizumab with pemetrexed and investigator-selected carboplatin or cisplatin. Arm B used pemetrexed with investigator-selected carboplatin or cisplatin, without atezolizumab. The study summary describes induction and maintenance phases. The available arm descriptions identify intravenous treatment, but some dosing text is incomplete in the registry record; further details should not be inferred from the abbreviated descriptions.

The primary outcome was investigator-assessed progression-free survival under RECIST v1.1. The analysis population was defined as all randomized patients, regardless of whether assigned treatment was received. The primary endpoint records 292 participants in Arm A and 286 in Arm B. Those are the posted analysis-group counts and need not be treated as a restatement of the overall enrollment figure.

Open-label assignment means participants and investigators were not masked to treatment assignment. The registry record does not report whether other outcome assessments or analyses used masking. Randomization supports a comparison of the assigned groups, while the open-label design is relevant when considering outcomes that involve investigator judgment or participant reporting. The registry record does not report the original sample-size justification or the full operational details of randomization.

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: The study is considered "Completed" because the planned study activities and analyses have been performed.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population was defined as all randomized patients, whether or not the patients received the assigned treatment.

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) as Assessed by the Investigator Using Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST v1.1), measured over Randomization up to approximately 39 months.

Progression-free survival is a time-to-event endpoint. For each participant, the recorded time begins at randomization and ends at the first occurrence of disease progression determined by the investigator using RECIST v1.1, or death from any cause. The event is whichever of those occurs first. Participants without a recorded event by the relevant analysis time may have follow-up that is censored, but the registry record does not describe the censoring rules or handling of incomplete follow-up.

The median is the time by which half of the analyzed group is estimated to have experienced the endpoint event, under the survival analysis. It describes the center of the event-time distribution without assuming that every participant experiences the event at the same rate or at the same time. In the posted results, median progression-free survival is reported as 7.7 months in Arm A and 5.2 months in Arm B.

Time-to-event endpoints are used because they incorporate both whether an event occurs and how long it takes to occur. They can also make use of follow-up information from participants who have not yet had an event at the analysis cutoff, subject to the analysis methods and censoring assumptions. The registry record names the endpoint definition and reports a log-rank analysis with a hazard ratio, but does not provide a detailed account of censoring, follow-up completeness, or the statistical model beyond those reported items.

7. Results Posted in the Registry

• Arm B (Carboplatin or Cisplatin + Pemetrexed) vs Arm A (Atezolizumab + Carboplatin or Cisplatin + Pemetrexed: hazard ratio 0.56 (95% CI 0.47–0.67), reported p < 0.001 (as reported in the registry).

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is time to an event, rather than a measurement taken at one fixed visit. The event was defined as investigator-assessed disease progression under RECIST v1.1 or death from any cause, whichever occurred first. Time began at randomization. A participant who had not experienced an event by the analysis cutoff could contribute follow-up up to the last known event-free time, depending on the censoring rules. The registry record does not report those detailed rules.

What does a median time-to-event estimate describe?

In general, a median time-to-event estimate is the point at which the estimated event-free proportion reaches one half. It is a summary of the distribution, not an arithmetic average of individual event times. Survival methods can account for participants whose follow-up ends before an event is observed, provided the required assumptions about censoring are appropriate. The posted medians are 7.7 months for Arm A and 5.2 months for Arm B. The registry record also gives 95% confidence intervals for each median.

What does the hazard ratio describe?

In general, a hazard is the instantaneous event rate among participants who have not yet experienced the event, considered over follow-up. A hazard ratio compares hazards between groups under a specified ordering. It is not the ratio of median times, and it does not directly state how many months an individual gains or loses. The sponsor-reported estimate is 0.562, with a 95% confidence interval from 0.471 to 0.671. The comparison is labeled Arm B versus Arm A in the registry record; because the numerator convention is not separately described, the estimate should be quoted with that label rather than silently reversing the groups.

What role does the log-rank method play?

The registry record identifies the log-rank method for the reported time-to-event comparison. In general, the log-rank test compares event experience across groups over follow-up, using the timing of events and the risk sets at those times. It does not reduce the comparison to a single endpoint measurement at a fixed visit. The record presents the test result as p < 0.001 and reports the hazard ratio with its confidence interval. Further details about model specification, stratification, or other adjustments are not reported in the registry record.

How should the confidence interval and p-value be read?

In general, a confidence interval describes uncertainty around an estimate under a statistical procedure and its assumptions. It is not a range that contains every participant’s result. The interval for the hazard ratio runs from 0.471 to 0.671; the intervals for the two medians are 6.7 to 8.5 months and 4.3 to 5.6 months. A p-value is calculated under a null model and describes how unusual the data or more extreme data would be under that model. It does not measure the probability that a treatment effect is real, and it does not by itself measure clinical importance.

Randomization is the design feature intended to make treatment groups comparable, on average, at the point of assignment. The primary population was the intention-to-treat population: all randomized patients, regardless of whether they received assigned treatment. This preserves the randomized grouping for the primary comparison. The registry record does not describe the handling of missing endpoint information, deviations from assigned treatment, or additional analysis populations.

The study was open-label. In general, knowledge of assignment can be relevant to outcomes requiring judgment or participant reporting. Here the primary endpoint included investigator-determined progression. RECIST v1.1 provides a stated assessment framework, but the registry record does not report whether assessment was independently reviewed or masked. Patient-reported measures are also listed as secondary outcomes, although their detailed results and analysis methods are not described in the registry entries.

The reported inference is distinct from planning illustrations based on the observed hazard ratio. Planning calculations use assumed design conditions to estimate how many events or participants might be needed to detect a chosen effect with a selected power. They are not a description of the trial’s actual observed power, and they do not establish the original trial design assumptions. The original sample-size justification and detailed statistical analysis plan are not reported in the registry record.

Multiplicity arises when several outcomes or comparisons are examined. In general, making many statistical tests can increase the chance of at least one small p-value under null effects, unless the analysis plan accounts for that testing. The registry record lists 15 outcome measures, 13 posted secondary outcomes, and 7 analyses, but does not report a multiplicity adjustment strategy. The primary endpoint’s reported p-value should therefore be read as the result for that stated analysis, not as evidence that all listed outcomes were tested or controlled in a particular way.

10. Confidence Intervals and Precision

The primary endpoint is reported with 95% confidence intervals for both group medians and the hazard ratio. Arm A has median progression-free survival of 7.7 months, with a 95% confidence interval from 6.7 to 8.5 months. Arm B has a median of 5.2 months, with a 95% confidence interval from 4.3 to 5.6 months. The hazard ratio is 0.562, with a 95% confidence interval from 0.471 to 0.671.

In general, a confidence interval communicates statistical uncertainty around an estimate under the analysis assumptions. A narrower interval indicates greater precision on that scale, while a wider interval indicates more uncertainty. The intervals for medians and the interval for the hazard ratio are on different scales and should not be compared as if they measured the same quantity. The median intervals describe uncertainty in estimated event times; the hazard-ratio interval describes uncertainty in a relative hazard measure.

A confidence interval is not a prediction interval for individual participants, and it does not imply that every plausible value within it is equally likely. Its coverage interpretation depends on the statistical procedure and assumptions. The registry record gives the interval endpoints but does not report additional details about their calculation, such as whether the median intervals were obtained using a particular survival-curve method.

The hazard-ratio interval does not include 1. The associated reported p-value is p < 0.001. These statistics are consistent with a difference under the stated analysis, but precision and statistical evidence do not answer every question about the size, relevance, durability, or safety of a treatment contrast. They also do not resolve limitations arising from the open-label design, missingness, multiplicity, or other unreported analysis details.

11. 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 total event counts, not participants per arm. They use a time-to-event planning method identified in the registry record as Schoenfeld. The calculations are illustrations based on the observed effect, not the trial’s original design justification. The original sample-size assumptions are not reported in the registry record.

The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated proportion of the observed effect. For planning at 100% of the observed effect, the figures are 95 total events for 80% power and 127 total events for 90% power. At 75% of the observed effect, the figures are 169 total events for 80% power and 226 total events for 90% power. At 50% of the observed effect, the figures are 379 total events for 80% power and 507 total events for 90% power.

In general, a power value describes the probability that a planned analysis will detect an effect of the specified size at the chosen significance level, if the assumptions used in the calculation hold. The 80% column means planning for an 80% chance of detecting that assumed effect; the 90% column means planning for a 90% chance. These are design targets for the illustration, not probabilities that the observed result is correct.

The pattern across the figures reflects a general planning principle: smaller effects are harder to detect, so more events are needed to attain the same power under otherwise similar assumptions. The listed event totals are not the number of randomized participants, and they should not be read as a reconstruction of the actual enrollment target. These calculations are not observed power.

12. 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 = 0.562, so ln(HR) = -0.5763.
2. d = 4 × (1.96 + 0.842)² / [ln(0.562)]² = 94.5, rounded up to 95 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 <- 0.562                              # 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(2657434)
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 = 95 (80% power), 127 (90% power)
 75% of observed effect: events = 169 (80% power), 226 (90% power)
 50% of observed effect: events = 379 (80% power), 507 (90% power)
Simulated power with 95 events: 0.763 (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.

13. 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 142 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 578 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 <- 5.2          # control-arm median, months (converted from the posted unit)
hr          <- 0.562          # 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: 92         p (1-sided)   0.0001
  Events: 43        ~HR at bound   0.3200
   Month: 15    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.56   0.0338
   IA 2: 67%                   Z   2.5114
      N: 142         p (1-sided)   0.0060
  Events: 85        ~HR at bound   0.5796
   Month: 24    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.56   0.5603
       Final                   Z   1.9930
      N: 142         p (1-sided)   0.0231
 Events: 128        ~HR at bound   0.7023
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.56   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

14. Analyses Reported by the Sponsor

The registry record reports the sponsor’s primary time-to-event analysis as a log-rank comparison with a hazard ratio of 0.562, a 95% confidence interval from 0.471 to 0.671, and p < 0.001. The comparison is labeled Arm B versus Arm A. The posted arm-specific medians are 5.2 months for Arm B and 7.7 months for Arm A, each with its own 95% confidence interval.

The available results identify this as the sponsor-reported analysis; they do not give a separate independent recalculation of the endpoint estimate. Therefore there is no competing recalculated hazard ratio to set against the sponsor’s result. The registry record does not flag a discrepancy. The reported comparison and its stated method are the appropriate basis for describing the posted inferential result.

Planning illustrations based on the observed effect answer a different question from the sponsor’s trial analysis. They show event counts associated with specified planning assumptions and power targets. They do not verify the reported analysis, replace the sponsor’s analysis, or provide the original study’s design rationale. The registry record does not report the complete statistical analysis plan or detailed model conventions beyond the listed method and result.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is explicitly defined as the intention-to-treat population, including all randomized patients whether or not they received assigned treatment. The endpoint is investigator-assessed progression-free survival from randomization to progression under RECIST v1.1 or death from any cause. This definition identifies the population and endpoint, but it does not fully specify how every analysis was conducted.

The registry record lists 15 outcome measures, 13 posted secondary outcomes, and 7 analyses. Secondary outcomes include overall survival rates at Year 1 and Year 2, investigator-assessed objective response and duration of response, patient-reported symptom measures, and minimum observed serum atezolizumab concentration. The details needed to determine which outcomes were part of a confirmatory testing sequence are not reported in the registry record.

Multiplicity refers, in general, to the statistical issue created by examining several hypotheses or endpoints. If many tests are conducted, the chance of at least one apparently unusual result can increase when all null hypotheses are true. A prespecified testing sequence or an adjustment procedure can address this issue, but the registry record does not report whether either was used. The primary endpoint result should be distinguished from conclusions about secondary outcomes, especially when their statistical results and multiplicity handling are not described.

Details of missing-data handling are not reported in the registry record. This includes the rules for incomplete progression assessments, loss to follow-up, censoring, and missing patient-reported outcomes. The record also does not report whether interim analyses were conducted, the stopping rules, or the full statistical analysis plan. These are unknowns rather than evidence that a particular procedure was or was not used.

The registry definition of the intention-to-treat population does not by itself explain how the analysis handled every participant’s follow-up or protocol deviations. Additional analysis populations, sensitivity analyses, subgroup analyses, and adjustment variables are not described in the available record. These omissions limit how fully the reported estimate can be independently reconstructed from the registry information.

16. 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 (5.8%), febrile neutropenia (4.1%), pyrexia (4.1%), anaemia (3.8%), thrombocytopenia (3.8%).

The registry record reports serious adverse event figures by safety group. In Arm B, 91 of 274 participants at risk are listed as affected by serious adverse events; in Arm A, the corresponding figures are 149 of 291. Other adverse events are listed for 255 of 274 participants at risk in Arm B and 275 of 291 in Arm A. The record also lists 189 deaths in Arm B and 190 in Arm A. These counts should be read with their stated group denominators and should not be treated as a causal comparison on their own.

The most frequently listed serious adverse event terms and their posted percentages are pneumonia, 5.8%; febrile neutropenia, 4.1%; pyrexia, 4.1%; anaemia, 3.8%; thrombocytopenia, 3.8%; and diarrhoea, 3.1%. The registry record does not provide the detailed event-level definitions, timing, exposure adjustment, or causal attribution needed to interpret these terms beyond their reported classification.

Counts of affected participants are not equivalent to counts of event episodes, and the registry’s at-risk group is the relevant denominator for the listed figures. The safety summaries do not establish that an event was caused by a study treatment. They also do not, by themselves, provide a complete comparison of treatment burden or risk over time.

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

The registry record describes a randomized comparison of two regimens in chemotherapy-naive participants with Stage IV non-squamous NSCLC. The primary endpoint was investigator-assessed progression-free survival. The posted medians are 7.7 months for the atezolizumab combination group and 5.2 months for the chemotherapy-only group. The sponsor-reported log-rank analysis gives a hazard ratio of 0.562, a 95% confidence interval from 0.471 to 0.671, and p < 0.001.

Those results indicate the observed group-level pattern and the statistical evidence reported for the primary comparison. They do not mean that every participant in one group had longer progression-free survival than every participant in the other, or that an individual’s outcome can be predicted from the group median. A median is a summary of a distribution, and the hazard ratio is a relative time-to-event measure. Neither one describes the full range of participant experiences.

The results concern progression-free survival as defined and assessed in this trial. They do not by themselves establish results for overall survival, objective response, duration of response, patient-reported symptoms, or other secondary outcomes. Although those outcomes are listed in the registry record, their detailed estimates are not included in the registry record for this result. The reported primary endpoint should not be used as a substitute for those outcome-specific findings.

The study was open-label, and progression was determined by investigators using RECIST v1.1. Randomization is an important design feature for comparing assigned groups, while open-label assessment is relevant context for an endpoint involving investigator judgment. The registry record does not report whether progression was independently reviewed or masked. It also does not report complete details about missing follow-up, censoring, multiplicity control, or the original sample-size justification.

The adverse event counts and listed serious event terms provide safety information as recorded, but they do not establish causation or offer a complete benefit-risk assessment. The registry results are trial-level evidence under the study’s eligibility criteria, treatment regimens, outcome definitions, and analysis. They do not guarantee an outcome for any individual or resolve questions not addressed by the reported data.

18. Why This Trial Matters Statistically

This trial illustrates the statistical distinction between an endpoint summary and a comparative time-to-event analysis. Median progression-free survival gives a recognizable summary in months for each group, while the hazard ratio and its confidence interval describe a relative contrast over follow-up under the reported analysis. These statistics answer related but different questions. A hazard ratio should not be interpreted as a difference between medians or converted into an individual time gain.

It also shows why the endpoint definition matters. Progression-free survival combines investigator-determined progression under RECIST v1.1 with death from any cause, counting whichever occurs first. The endpoint therefore depends on both the event definition and the procedures for assessment and follow-up. The registry record identifies the definition and log-rank method, while leaving several operational analysis details unreported.

The randomized parallel-group design and the intention-to-treat population provide a clear framework for the primary comparison: participants are analyzed in their randomized groups, whether or not they received assigned treatment. At the same time, the open-label design and investigator assessment are relevant when interpreting the endpoint. Statistical evidence should be considered alongside design and measurement, not in isolation.

Finally, planning figures based on the observed effect demonstrate how a smaller target effect requires more events to achieve the same planned power under the stated assumptions. Those illustrations are distinct from the actual study design and from the observed result. The trial is therefore useful for understanding how design, endpoint definition, uncertainty, and planning calculations fit together without conflating them.

19. 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 the original sample-size justification or the assumptions used to set the trial’s enrollment target. The planning illustrations based on the observed effect cannot fill that gap: they use stated illustrative assumptions and are not a reconstruction of the original design.

The primary endpoint was assessed by investigators in an open-label study. The record states that RECIST v1.1 was used, but whether progression assessments received independent or masked review is not reported in the registry record. The potential relevance of this is specific to an outcome that includes investigator-determined progression.

Further details about the time-to-event analysis are also not reported in the registry record. These include censoring rules, missing endpoint data, follow-up completeness, any stratification or adjustment variables, and the convention used for the numerator and denominator of the hazard ratio. The comparison label is given as Arm B versus Arm A, so the estimate should be cited with that label rather than assuming an undocumented ordering convention.

The record lists multiple outcome measures and analyses but does not report a multiplicity strategy, interim analyses, stopping rules, or the full statistical analysis plan. Detailed results for the listed secondary outcomes are not included in the information. The safety figures are aggregate counts and listed terms; event timing, exposure-adjusted rates, and detailed attribution are not reported.

These limits affect how completely the posted result can be reconstructed and how broadly it can be interpreted. They do not change the values reported for the primary endpoint, but they leave important aspects of design and analysis uncertain in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Atezolizumab in Combination With Carboplatin or Cisplatin + Pemetrexed Compared With Carboplatin or Cisplatin + Pemetrexed in Participants Who Are Chemotherapy-Naive and Have Stage IV Non-Squamous Non-Small Cell Lung Cancer (NSCLC) (IMpower 132) — NCT02657434.
• Registry record last updated 2023-11-21; status last verified 2023-11.
• Results first posted 2020-10-09.
• 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.

23. Record Summary

NCT02657434 is a completed randomized, open-label, parallel-group Phase III study of atezolizumab plus pemetrexed and investigator-selected carboplatin or cisplatin versus pemetrexed with investigator-selected carboplatin or cisplatin. It enrolled 578 chemotherapy-naive participants with Stage IV non-squamous NSCLC. The primary endpoint was investigator-assessed progression-free survival under RECIST v1.1.

Median progression-free survival was 7.7 months in Arm A and 5.2 months in Arm B. The sponsor-reported log-rank analysis gave a hazard ratio of 0.562, with a 95% confidence interval from 0.471 to 0.671 and p < 0.001. The registry record also lists secondary outcomes and safety summaries, while several analysis details—including missing-data handling, multiplicity procedures, and the original sample-size justification—are not reported.