A Study of Atezolizumab in Combination With Carboplatin Plus (+) Nab-Paclitaxel Compared With Carboplatin+Nab-Paclitaxel in Participants With Stage IV Non-Squamous Non-Small Cell Lung Cancer (NSCLC): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Atezolizumab in Combination With Carboplatin Plus (+) Nab-Paclitaxel Compared With Carboplatin+Nab-Paclitaxel in Participants With Stage IV Non-Squamous Non-Small Cell Lung Cancer (NSCLC) (NCT02367781), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS) as Determined by the Investigator Using Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST v1.1) in the ITT-WT Population.

2. Clinical Question

3. Trial Design

This was a Phase III, multicenter, randomized, open-label, parallel-group study. It compared atezolizumab plus carboplatin and nab-paclitaxel with carboplatin and nab-paclitaxel in chemotherapy-naive participants with stage IV non-squamous non-small cell lung cancer. The registry lists enrollment of 723 and describes allocation in a 2:1 ratio to Arm A and Arm B. The record is marked completed.

Because masking was listed as none, participants and study personnel were not masked to assigned treatment. The primary endpoint was progression-free survival assessed by investigators using RECIST v1.1 in the ITT-WT population. That population excluded participants with an activating EGFR mutation or ALK translocation from the ITT population. The primary endpoint timeframe is described as up to approximately 35 months after the first participant was enrolled.

The induction descriptions specify treatment on a 21-day cycle. In Arm A, atezolizumab and carboplatin were given on Day 1 and nab-paclitaxel on Days 1, 8, and 15. In Arm B, carboplatin was given on Day 1 and nab-paclitaxel on Days 1, 8, and 15. Both descriptions refer to 4 or 6 induction cycles, with different stopping conditions. The treatment description for Arm B also mentions best supportive care during maintenance; further details of the Arm A maintenance description are not reported in the registry record.

The record lists secondary outcomes that include progression-free survival, overall survival, objective response, duration of response, event-free rates, and patient-reported lung cancer symptoms. It reports 18 outcome measures and 25 analyses. The original sample-size justification, the detailed randomization procedure, and the protocol’s prespecified statistical plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Participants in this study included: histologically or cytologically confirmed, Stage IV non-squamous NSCLC; and no prior treatment for Stage IV non-squamous NSCLC. At the time of study completion a few participants that were still on maintenance treatment with atezolizumab were moved to another study, Post-Trial Access Program, or commercial use. Therefore, the reason for discontinuation was entered "Study terminated by Sponsor" for these participants.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT- WT population was defined as the ITT population excluding participants with an activating EGFR mutation or ALK translocation.

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 Determined by the Investigator Using Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST v1.1) in the ITT-WT Population, measured over Up to approximately 35 months after first patient enrolled.

The primary endpoint was progression-free survival in the ITT-WT population, assessed by the investigator using RECIST v1.1. It measures the time from randomization until the first documented disease progression or death from any cause, whichever occurs first. Participants who have not had either event by the end of observed follow-up are generally treated as censored in time-to-event analyses; the specific censoring rules used for this study are not reported in the registry record.

Progression-free survival is used to capture both tumor progression and death in a single time-to-event outcome. This can describe how long participants remain alive without documented progression, while avoiding the need to wait for death in every participant. It is distinct from overall survival, which counts time until death, and from objective response, which records whether a complete or partial response was observed.

The registry reports median progression-free survival for each group and a hazard ratio from a log-rank analysis. A median is the time by which half of the relevant group has experienced the event, subject to the time-to-event analysis. It does not describe every participant’s experience, nor does a difference between group medians alone quantify the full time-to-event contrast. The hazard ratio summarizes the relative event rate over follow-up under the model and analysis used; it is not a difference in median months.

Investigator assessment and the open-label design are important context for interpreting this endpoint. The registry identifies RECIST v1.1 as the assessment standard, but assessment timing, independent review, and detailed rules for handling missing or unevaluable assessments are not reported in the registry record.

7. Results Posted in the Registry

• Arm A (Atezolizumab+Nab-Paclitaxel+Carboplatin) vs Arm B (Nab-Paclitaxel+Carboplatin): hazard ratio 0.64 (95% CI 0.54–0.76), reported p < 0.001 (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.

OS as Determined by the Investigator Using Recist v1.1 in the ITT Population

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Arm A (Atezolizumab+Nab-Paclitaxel+Carboplatin) vs Arm B (Nab-Paclitaxel+Carboplatin): hazard ratio 0.84 (95% CI 0.69–1.02), reported p = 0.073 (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 A (Atezolizumab+Nab-Paclitaxel+Carboplatin) vs Arm B (Nab-Paclitaxel+Carboplatin) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With an Objective Response (OR) (Complete Response [CR] or Partial Response [PR]) as Determined by the Investigator Using RECIST v1.1 in the ITT-WT Population

• 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 B (Nab-Paclitaxel+Carboplatin): 41.0% (93/227) versus 60.2% (272/452) on control; risk difference -19.2 percentage points (95% CI -27.0 to -11.4), risk ratio 0.68 (0.57–0.81); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm B (Nab-Paclitaxel+Carboplatin) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time to Deterioration (TTD) in Patient-Reported Lung Cancer Symptoms in the ITT-WT Population

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Arm A (Atezolizumab+Nab-Paclitaxel+Carboplatin) vs Arm B (Nab-Paclitaxel+Carboplatin): hazard ratio 0.89 (95% CI 0.71–1.12), reported p = 0.334 (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 A (Atezolizumab+Nab-Paclitaxel+Carboplatin) vs Arm B (Nab-Paclitaxel+Carboplatin) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span several distinct domains: overall survival, progression-free survival in additional analysis populations, objective response, duration of response, event-free rates, and patient-reported symptoms. They do not all measure the same construct, and they include different analysis populations and follow-up periods. The posted overall-survival and objective-response results offer context alongside the primary progression-free-survival finding, while the symptom deterioration result addresses a patient-reported outcome rather than tumor progression or death.

Across these outcomes, the strength of statistical evidence is not uniform. Some sponsor-reported comparisons have confidence intervals that include the null value for their relative measure, while other reported comparisons show stronger separation from their null. This variation is not inherently inconsistent: outcomes can differ in event frequency, measurement, population, follow-up, and statistical precision. The secondary results should be interpreted as complementary evidence, not as interchangeable confirmation of a single endpoint.

The registry lists 18 outcome measures and 25 analyses, and several outcomes are examined in more than one population. When many comparisons are considered, the chance of seeing at least one small p-value by chance can increase. In general, multiplicity procedures can control that risk by setting a testing order or adjusting inference. The registry record does not report enough detail to determine whether or how the secondary analyses were adjusted for multiple testing. Unadjusted secondary p-values therefore carry less confirmatory weight than a prespecified primary analysis with a clear multiplicity plan.

Secondary outcomes can still be informative, especially when their definitions and populations are considered carefully. They can help describe the range of observed outcomes, but they should not be used to override the primary analysis or to make stronger claims than their precision and analysis status support. Their results are most useful when treated as evidence with varying degrees of uncertainty, rather than as a single overall verdict.

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

• PFS as Determined by the Investigator Using Recist v1.1 in the ITT Population, PD-L1 Expression Population, and PD-L1 Expression WT Population
• OS as Determined by the Investigator Using Recist v1.1 in the ITT Population
• OS as Determined by the Investigator Using RECIST v1.1 in the PD-L1 Expression Population and PD-L1 Expression WT Population
• Percentage of Participants With an Objective Response (OR) (Complete Response [CR] or Partial Response [PR]) as Determined by the Investigator Using RECIST v1.1 in the ITT-WT Population
• Percentage of Participants With an Objective Response (OR) (Complete Response [CR] or Partial Response [PR]) as Determined by the Investigator Using RECIST v1.1 in the ITT Population, PD-L1 Expression Population, and PD-L1 Expression WT Population
• Duration of Response (DOR) as Determined by the Investigator Using RECIST v1.1 in ITT-WT Population, ITT Population, and PD-L1 Expression Population and PD-L1 Expression WT Population
• Event Free Rate (%) at Year 1 and 2 in ITT-WT Population and ITT Population
• Event Free Rate (%) at Year 1 and 2 in PD-L1 Expression Population and PD-L1 Expression WT Population

9. Statistical Interpretation

10. Statistical Methods Explained

What does the hazard ratio describe?

In general, a hazard ratio compares the event rates between groups over follow-up. For this trial’s primary outcome, the event is documented progression or death, whichever occurs first. A hazard ratio of 1 corresponds to equal hazards under the comparison; a value below 1 indicates a lower estimated hazard in the first-listed group, and a value above 1 indicates a higher estimated hazard. This is a relative rate measure and should not be read as a ratio of median survival times or as an absolute probability difference. Its interpretation can depend on how hazards behave over time, and the registry record does not report an assessment of that assumption.

Why is a log-rank analysis used?

In general, the log-rank test compares time-to-event experience while accounting for the fact that participants can have different lengths of follow-up. It uses the timing of events and information from participants who remain under observation without an event. Such participants contribute information until their last known observation, after which they may be censored under the analysis rules. The registry identifies the log-rank method for the reported hazard-ratio analyses, but does not report the full model specification, censoring rules, or diagnostics.

For the primary comparison, the sponsor reports a hazard ratio of 0.639 and a 95% confidence interval of 0.536 to 0.763, with p <.0001. These are the inferential statistics to use when describing the primary time-to-event comparison. The median values are useful descriptive summaries, but they do not replace the hazard-ratio analysis.

What does a confidence interval contribute?

In general, a confidence interval gives a range of values compatible with the observed data and the analysis procedure, under its assumptions. It conveys uncertainty around an estimate rather than a guarantee that the true value lies inside the particular interval. For a hazard ratio, an interval that includes 1 is compatible with equal hazards at the corresponding confidence level; an interval entirely below 1 is not. This is one way to assess the strength and precision of a relative time-to-event estimate, alongside the point estimate and p-value.

The registry reports 95% confidence intervals for the primary median estimates and hazard ratio. The intervals around the two medians are summaries for each group separately; their overlap or non-overlap is not a substitute for the formal comparison. The confidence interval for the hazard ratio directly describes uncertainty in that relative estimate.

How should p-values be read?

In general, a p-value measures how unusual the observed data, or more extreme data, would be if the specified null hypothesis and analysis assumptions were true. 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 comparison’s p <.0001 is the sponsor-reported result. The registry identifies a superiority analysis, but the detailed testing sequence and any adjustment for multiple comparisons are not reported in the registry record.

What is different about the recalculated binary result?

For a binary outcome such as objective response, a risk difference compares the proportions with the outcome in two groups. The registry’s sponsor-reported analysis for response in the ITT-WT population used the Cochran-Mantel-Haenszel method and reports a difference in response rate of 19.21, with a 95% confidence interval of 11.05 to 27.37 and p <.0001. The accompanying unadjusted re-calculation uses posted summary counts and is a simple comparison rather than a replacement for that sponsor analysis. The registry’s adjustment method and the unadjusted calculation need not produce identical estimates or uncertainty intervals.

In general, adjustment can account for stratification or other design features specified in an analysis. A simple unadjusted calculation does not necessarily reproduce those features. The registry identifies the sponsor method for the reported response analysis, but the detailed strata and model implementation are not reported in the registry record. For this reason, the sponsor’s own analysis is the principal result to cite when discussing that endpoint.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. If a model assumes less variability than the data contain, its standard errors can be too small and its confidence intervals too narrow. This is a general statistical concern, not a reported feature of this trial. The registry record does not report an over-dispersion assessment or a correction for it.

More broadly, all model-based estimates rely on assumptions. For time-to-event analyses, these can include how censoring is handled and whether the summary measure is appropriate for the event pattern. The registry lists the method and results but does not provide enough detail to independently evaluate every assumption. The interpretation should therefore remain tied to the analysis as reported.

11. Confidence Intervals and Precision

The primary median estimates are 7.0 months in Arm A and 5.5 months in Arm B. Their 95% confidence intervals are 6.3 to 7.3 months and 4.4 to 5.9 months, respectively. These intervals describe uncertainty in each group’s median estimate. They should not be interpreted as ranges containing most individual participants’ progression-free survival times; individual outcomes can be more varied.

The primary relative estimate is a hazard ratio of 0.639, with a 95% confidence interval of 0.536 to 0.763. The interval does not include 1, the value corresponding to equal hazards in the general interpretation of a hazard ratio. Its width gives a sense of precision for the relative estimate, but does not account for biases or limitations outside the statistical interval, including possible measurement issues in an open-label study.

A confidence interval is not a probability statement about the specific true effect after the data have been observed. In general, it describes the performance of an interval procedure across repeated studies under its assumptions. The interval also does not show how much individual outcomes vary, whether an effect matters to participants, or whether all subgroups experience similar results.

Other estimates have different precision. For overall survival, the hazard-ratio interval is 0.689 to 1.017, which includes 1. For time to deterioration in patient-reported symptoms, the interval is 0.711 to 1.123, also including 1. These intervals are compatible with a wider range of relative effects than a point estimate alone suggests. The registry does not report a common precision measure that would make all endpoints directly comparable, and differences in populations, event definitions, follow-up, and analysis also matter.

Confidence intervals quantify sampling uncertainty under the analysis; they do not address missing-data mechanisms, endpoint assessment choices, multiplicity, or departures from model assumptions. Details on those issues are not reported in the registry record, so the intervals should be read as statistical precision conditional on the reported analyses rather than as a complete measure of certainty.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For time-to-event outcomes, the figures are total events needed. For other outcomes, they are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each illustration targets the stated fraction of the observed effect. The original trial’s sample-size justification is not reported in the registry record.

The 80% power column describes the planning number of events or participants that would correspond to an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target chance of detecting that same specified effect. These are prospective planning concepts, not guarantees of what a completed study will detect.

Rows for 100% of the observed effect use the effect estimated in the posted results; rows for 75% and 50% of that effect illustrate smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more events or participants under the same planning assumptions. A time-to-event figure should not be read as a count per arm, while a non-time-to-event figure should not be read as a total across both arms.

These calculations are not observed power. They are illustrations of the sample sizes associated with chosen effect sizes and conventional power targets, not a retrospective measure of whether the trial had adequate power after its results were known. The actual study allocation, endpoint population, follow-up, event accumulation, and analysis may differ from the simplified planning assumptions used for the illustrations.

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 = 0.639, so ln(HR) = -0.4479.
2. d = 4 × (1.96 + 0.842)² / [ln(0.639)]² = 156.5, rounded up to 157 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 <- 0.639                              # 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(2367781)
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 = 157 (80% power), 210 (90% power)
 75% of observed effect: events = 279 (80% power), 373 (90% power)
 50% of observed effect: events = 627 (80% power), 839 (90% power)
Simulated power with 157 events: 0.807 (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 235 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 723 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 <- 5.5          # control-arm median, months (converted from the posted unit)
hr          <- 0.639          # 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: 150         p (1-sided)   0.0001
  Events: 71        ~HR at bound   0.4129
   Month: 15    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.64   0.0338
   IA 2: 67%                   Z   2.5114
      N: 236         p (1-sided)   0.0060
 Events: 141        ~HR at bound   0.6549
   Month: 24    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.64   0.5603
       Final                   Z   1.9930
      N: 236         p (1-sided)   0.0231
 Events: 212        ~HR at bound   0.7601
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.64   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 sponsor-reported analysis is a log-rank hazard ratio of 0.639, with a 95% confidence interval of 0.536 to 0.763 and p <.0001. Those are the reported inferential results to use when describing the primary comparison. The registry also reports the group medians, but the medians alone are not a re-calculation of the sponsor’s relative time-to-event analysis.

For the objective-response endpoint, the sponsor reports a Cochran-Mantel-Haenszel difference in response rate of 19.21, with a 95% confidence interval of 11.05 to 27.37 and p <.0001. A simple unadjusted re-calculation from the posted summary counts is a different analysis and does not replace the sponsor’s adjusted comparison. The record does not flag a discrepancy between the posted sponsor analysis and the corresponding reported comparison results.

In general, an unadjusted calculation can be useful as a transparent check of summary data, while the sponsor analysis may incorporate the planned method or design features. When both are available, the sponsor’s own analysis takes precedence for reporting the trial’s inferential conclusion, especially where the methods differ. The details needed to reproduce all aspects of the sponsor’s analyses are not reported in the registry record.

16. Multiplicity, Missing Data and Analysis Populations

The registry record identifies progression-free survival in the ITT-WT population as the primary endpoint and lists numerous secondary outcomes and analyses. It also includes analyses across the ITT, PD-L1 expression, PD-L1 expression WT, and ITT-WT populations. Examining multiple endpoints and populations creates a multiplicity issue: even when no underlying effect exists for a set of comparisons, the chance of one or more apparently unusual results can grow as the number of tests increases.

In general, a prespecified testing hierarchy or a multiplicity adjustment can help control the overall false-positive risk. The registry record does not report a detailed testing hierarchy, the family of hypotheses used for adjustment, or whether secondary p-values were adjusted. The original statistical analysis plan is not reported in the registry record. Consequently, secondary p-values should be treated cautiously and should not automatically be interpreted as confirmatory evidence.

Missing-data handling is also not reported in sufficient detail. The record gives endpoint definitions and analysis populations, but does not describe rules for missing assessments, loss to follow-up, censoring, or sensitivity analyses for departures from the main missing-data assumptions. In general, time-to-event methods can accommodate participants whose follow-up ends before an event through censoring, but valid interpretation depends on how censoring arises and how it is handled. Those study-specific details are not reported in the registry record.

Population definitions differ across outcomes. The primary ITT-WT population excludes participants with an activating EGFR mutation or ALK translocation from the ITT population. Other secondary analyses use ITT or PD-L1-defined populations. These distinctions matter because estimates from one population do not necessarily describe another. The registry record does not provide a complete account of all analysis-population rules, subgroup hypotheses, or sensitivity analyses. These gaps limit independent evaluation of the full inferential strategy, without changing the fact that the posted primary result is the sponsor-reported comparison for the specified ITT-WT population.

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 (9.9%), anaemia (4.0%), chronic obstructive pulmonary disease (3.8%), pulmonary embolism (3.6%), neutropenia (3.0%).

The registry reports serious adverse events by treatment-related safety groups, including Arm A, Arm B participants without crossover, and Arm B participants with crossover after receiving atezolizumab monotherapy. In Arm A, 252 of 473 participants at risk had a serious adverse event. The corresponding figures are 63 of 131 for Arm B without crossover and 24 of 101 for Arm B with crossover. These counts describe the registry’s listed groups; the crossover groups should not be combined casually because they represent different treatment exposure histories.

The most frequently listed serious adverse-event terms include pneumonia at 9.9%, anaemia at 4.0%, chronic obstructive pulmonary disease at 3.8%, pulmonary embolism at 3.6%, neutropenia at 3.0%, and diarrhoea at 3.0%. The record also lists deaths in the safety groups, but those counts alone do not establish cause or treatment attribution. The registry does not provide enough detail to determine how every event was adjudicated or to compare event duration, severity grades, or exposure-adjusted rates.

Serious adverse-event counts are descriptive safety information, not a randomized efficacy comparison. Differences in group size, crossover, treatment exposure, follow-up, and attribution can affect interpretation. These figures should be read as reported safety events in the specified groups, not as proof that a treatment caused or prevented an event.

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

The primary analysis describes progression-free survival in a defined population: the ITT population excluding participants with an activating EGFR mutation or ALK translocation. The registry reports longer median progression-free survival for Arm A than Arm B and a hazard ratio below 1, with a 95% confidence interval below 1 and p <.0001. Statistically, these results support a difference between the groups under the reported analysis. They do not establish that every participant had a better outcome, nor do they describe the experience of people outside the analyzed population.

The hazard ratio is a relative summary of event rates over follow-up. It is not the probability that a participant will progress, the number of months gained by each participant, or a direct measure of quality of life. The medians summarize the time-to-event distributions but do not capture the full distribution of outcomes. The response, overall-survival, and symptom endpoints address different questions and should be interpreted according to their own definitions and analyses.

Statistical evidence is not the same as clinical importance. The registry results and confidence intervals can describe the size and uncertainty of estimates, but clinical importance also depends on context not established by these statistics alone. No medical recommendation follows from the reported comparisons. Decisions about care require individualized clinical judgment and evidence beyond the registry summary.

The study was open-label and used investigator assessment for the primary endpoint. These features do not invalidate the randomized comparison, but they are relevant when considering measurement and potential bias. The registry record does not report all details needed to evaluate assessment procedures, missing data, crossover effects, or the prespecified multiplicity plan. The results therefore answer the trial’s stated comparison as recorded, while leaving some methodological questions unresolved.

Finally, the findings are specific to the studied treatment regimens, participant eligibility, outcome definitions, and analysis populations. They should not be generalized automatically to other disease stages, tumor subtypes, treatment settings, or populations that were not represented by the relevant analysis.

19. Why This Trial Matters Statistically

This trial is statistically informative because it uses random allocation to compare a combination regimen with the chemotherapy comparator in a Phase III, multicenter study. Randomization is intended, in general, to reduce systematic differences between treatment groups at baseline. The open-label design and investigator-assessed primary endpoint remain important context for how progression was measured and interpreted.

The primary endpoint combines documented progression and death, providing a time-to-event measure that uses more information than a single outcome assessment at one fixed time. The registry reports medians alongside a hazard ratio and confidence interval, making it possible to distinguish descriptive group summaries from the relative comparison. The primary confidence interval is informative about statistical precision, rather than relying on a p-value alone.

The record also illustrates why population definitions matter. The primary result applies to the ITT-WT population, which excludes participants with an activating EGFR mutation or ALK translocation, while secondary analyses use other populations. A result should be attached to its stated population rather than treated as a universal estimate for all participants or all people with the disease.

At the same time, the set of secondary endpoints and analyses raises familiar statistical concerns about multiplicity and interpretation. Multiple outcomes can provide a broader view of efficacy and patient experience, but they also make it important to know which tests were prespecified and how false-positive risk was controlled. Those plan details are not reported in the registry record. The trial is therefore a useful case for reading the primary estimate, its uncertainty, and secondary evidence separately, while recognizing what the public record does not establish.

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.

Several limitations are specific to the information recorded for this trial. The study was open-label, and the primary progression-free-survival endpoint was assessed by investigators. The registry identifies RECIST v1.1 but does not report whether independent central review was used, how assessment timing was standardized, or how disagreements and unevaluable scans were handled. These omissions limit independent evaluation of potential assessment bias.

The primary analysis is restricted to the ITT-WT population, which excludes participants with an activating EGFR mutation or ALK translocation. This makes the population definition essential when applying the result; the estimate is not automatically representative of the excluded participants. Secondary outcomes use other populations, and those estimates should not be compared without accounting for their different eligibility and analysis rules.

The record lists crossover participants in the Arm B safety information, including participants who received atezolizumab monotherapy after crossover. Crossover can complicate interpretation of overall survival because later treatment exposure may differ from initial assignment. The registry record does not report enough detail about crossover timing, eligibility, or its handling in the overall-survival analysis to quantify that issue.

The detailed statistical analysis plan, sample-size justification, missing-data procedures, multiplicity strategy, and sensitivity analyses are not reported in the registry record. Their absence limits assessment of how fully the posted results follow a prespecified inferential plan. The registry also does not supply enough information to judge all model assumptions or to evaluate the robustness of results to alternative methods.

Finally, several analysis populations, outcomes, and comparisons are listed. The resulting secondary evidence needs to be interpreted in light of multiple testing and differing endpoint definitions. These limitations concern the scope and interpretability of the posted record; they do not change the reported numerical estimates.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Atezolizumab in Combination With Carboplatin Plus (+) Nab-Paclitaxel Compared With Carboplatin+Nab-Paclitaxel in Participants With Stage IV Non-Squamous Non-Small Cell Lung Cancer (NSCLC) — NCT02367781.
• Registry record last updated 2021-08-09; status last verified 2021-07.
• Results first posted 2019-04-03.
• 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 Phase III, multicenter, randomized, open-label, parallel-group study of atezolizumab plus carboplatin and nab-paclitaxel compared with carboplatin and nab-paclitaxel in chemotherapy-naive participants with stage IV non-squamous non-small cell lung cancer. Enrollment is listed as 723, with a 2:1 randomization ratio.

The primary endpoint was investigator-assessed progression-free survival by RECIST v1.1 in the ITT-WT population. The registry reports median values of 7.0 months and 5.5 months, and a sponsor-reported hazard ratio of 0.639 with a 95% confidence interval of 0.536 to 0.763 and p <.0001. The record also includes secondary efficacy and safety outcomes, but does not report the complete statistical plan, original sample-size justification, or detailed missing-data and multiplicity procedures.