Study to Assess Safety and Efficacy of Atezolizumab (MPDL3280A) Compared to Best Supportive Care Following Chemotherapy in Patients With Lung Cancer [IMpower010]: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess Safety and Efficacy of Atezolizumab (MPDL3280A) Compared to Best Supportive Care Following Chemotherapy in Patients With Lung Cancer [IMpower010] (NCT02486718), a randomized phase 3 study. The primary outcome is Disease-Free Survival (DFS) in Intent-to-treat (ITT) Population.

2. Clinical Question

The trial addresses a treatment question after surgery and adjuvant chemotherapy, rather than a question about initial treatment of unresected disease. Participants were randomized after completing up to four cycles of cisplatin-based chemotherapy. The chemotherapy regimens included cisplatin with vinorelbine, docetaxel, gemcitabine, or pemetrexed; pemetrexed was specified for non-squamous disease only. The arm descriptions indicate that the enrollment-phase chemotherapy could stop earlier for unacceptable toxicity, disease relapse, or a participant's decision to discontinue.

The randomized comparison is between a planned course of atezolizumab and best supportive care. It is not a comparison of chemotherapy against no chemotherapy: both groups received the enrollment-phase chemotherapy described in the record. The primary analysis population is defined by randomization, not by whether each participant completed the assigned post-randomization treatment.

The primary endpoint captures recurrence or death over time, while the registry also lists overall survival and disease-free rates at specified years as secondary outcomes. The principal reported comparison is a hazard ratio from a log-rank analysis. Those summaries answer related but distinct questions: the median describes a point on each group's estimated time-to-event curve, while the hazard ratio summarizes the relative event rate over the analysis period under the interpretation of that model.

3. Trial Design

NCT02486718 is a Phase III randomized, open-label, parallel-group study sponsored by Hoffmann-La Roche. Its stated purpose was to investigate the efficacy and safety of atezolizumab compared with best supportive care after adjuvant cisplatin-based chemotherapy in completely resected Stage IB-IIIA non-small cell lung cancer. The registry lists an enrollment of 1280 and a completed status.

Participants entered an enrollment phase involving up to four 21-day cycles of cisplatin-based chemotherapy. Following that phase, the study randomized participants in a 1:1 ratio to atezolizumab or best supportive care. The atezolizumab group was scheduled to receive 16 cycles, with each cycle lasting 21 days. The comparator group received best supportive care. The arm descriptions list the same chemotherapy options during enrollment for both groups, including cisplatin with one of several additional agents; pemetrexed was limited to non-squamous non-small cell lung cancer.

The study was open-label, so masking was not used. The primary endpoint was disease-free survival in the intent-to-treat population, assessed by the investigator. That population included all randomized participants with resected Stage IB tumors at least 4 centimetres through Stage IIIA disease, irrespective of whether assigned treatment was received. The primary endpoint timeframe is listed as up to 95 months.

The primary result includes 507 participants in the atezolizumab group and 498 in the best-supportive-care group. These are the group sizes associated with the posted primary endpoint, while the registry's overall enrollment figure is 1280. The record does not explain the relationship between those totals. The statistical justification for the original enrollment target, the original design assumptions, and any planned interim analyses are not reported in the registry record. A detailed schedule of follow-up assessments and the rules for censoring are also not reported in the registry record.

The listed secondary outcomes include overall survival and disease-free rates at Year 3 and Year 5 in different populations, including Stage II-IIIA and PD-L1-defined groups. Twelve secondary outcomes are indicated as posted, and the record indicates 15 outcome measures and 10 analyses. The record does not describe a hierarchy among secondary outcomes or a multiplicity-adjustment strategy.

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 consists of 2 phases, an enrollment phase in which participants received up to 4 cycles of adjuvant cisplatin-based chemotherapy followed by randomized phase in which eligible participants were randomized to receive atezolizumab or best supportive care (BSC) i.e.no treatment.

Enrollment Phase

Reasons for not completing this period:

Randomized Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized ITT population was defined as all randomized participants with resected Stage IB \[tumors ≥ 4 centimetres (cm)\]-IIIA NSCLC whether or not the participant 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.

Population: Enrolled population was defined as all eligible participants who were enrolled in the enrollment phase, regardless if they are subsequently randomized or not.

6. Primary Endpoint

The registry lists the primary outcome as Disease-Free Survival (DFS) in Intent-to-treat (ITT) Population, measured over Up to 95 months.

Disease-free survival is a time-to-event endpoint. In this study, the clock began at randomization. An event was the first investigator-determined recurrence of non-small cell lung cancer, a new primary non-small cell lung cancer, or death. Counting the first of these events gives the endpoint a clear clinical time origin and avoids treating different event types as if they had to occur together.

The registry says Kaplan-Meier methodology was used to estimate median disease-free survival in each treatment group. The median is the time at which the estimated proportion remaining event-free reaches one half. It gives an interpretable summary of the estimated event-time distribution, although it does not describe every feature of that distribution. The recorded median was 65.6 months for atezolizumab, with a reported lower confidence limit of 52.4 months and no upper limit reported in the registry record. For best supportive care, the median was 47.8 months, with a 95% confidence interval from 37.0 to 65.8 months.

Time-to-event methods are useful when participants have different lengths of observation or have not experienced the event by the end of their available follow-up. Such participants can contribute information until their last known event-free time; the statistical treatment of that incomplete observation depends on censoring rules. The registry identifies Kaplan-Meier estimation but does not report the detailed censoring rules or the handling of missing endpoint assessments.

The primary comparison is also reported as a hazard ratio, estimated with a log-rank method. A hazard ratio uses event timing across follow-up rather than comparing only the two medians. It therefore complements the median estimates, but the registry record does not report a proportional-hazards assessment or other details needed to assess the shape of the relative effect over time.

7. Results Posted in the Registry

• Atezolizumab vs Best Supportive Care (BSC): hazard ratio 0.85 (95% CI 0.71–1.01), reported p = 0.068 (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.

Disease-free Rate at Year 3 in ITT 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:
  • Atezolizumab: 61.3% (311/507) versus 55.4% (276/498) on control; risk difference 5.9 percentage points (95% CI -0.2 to 12.0), risk ratio 1.11 (1.00–1.23); unadjusted two-proportion z-test p = 0.057.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atezolizumab and the control. The interval gives the range of effects that remain compatible with the data.

Disease-free Rate at Year 3 in All Randomized Stage II-IIIA 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:
  • Atezolizumab: 59.3% (262/442) versus 52.7% (232/440) on control; risk difference 6.5 percentage points (95% CI 0.0 to 13.1), risk ratio 1.12 (1.00–1.26); unadjusted two-proportion z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Atezolizumab and the control. The interval gives the range of effects that remain compatible with the data.

Disease-free Rate at Year 3 in PD-L1 (SP263 ≥ 1% TC) Subpopulation Within the Stage II-IIIA 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:
  • Atezolizumab: 62.9% (156/248) versus 52.2% (119/228) on control; risk difference 10.7 percentage points (95% CI 1.9 to 19.6), risk ratio 1.21 (1.03–1.41); unadjusted two-proportion z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Atezolizumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary disease-free-rate results reported for Year 3 have point estimates that lean toward atezolizumab across the listed overall and subgroup populations. The amount of uncertainty varies by population: some reported intervals include a no-difference value, while the PD-L1-defined Stage II-IIIA result is more separated from that value in its reported interval. This broad pattern is directionally consistent with the primary hazard-ratio point estimate, but it is not a substitute for the primary time-to-event analysis.

These outcomes are related to the primary endpoint because they describe disease-free status at a specified time rather than the full time-to-event experience. A rate at a single year does not use the timing of every event in the same way as a Kaplan-Meier curve and hazard-ratio analysis. Results across different populations also need not have the same precision, since the populations and available information differ.

The record lists additional secondary outcomes, including overall survival and Year 5 disease-free rates, but the results included in the record do not give numerical estimates for every listed outcome. Unreported values should not be inferred from the Year 3 pattern. The record also does not report a statistical hierarchy or a multiplicity-adjustment strategy.

In general, testing several outcomes and subgroups creates more opportunities for chance findings. Without a reported adjustment or prespecified hierarchy, unadjusted secondary evidence carries less weight than the primary analysis and should be considered supportive or exploratory. Subgroup estimates do not demonstrate that treatment effects truly differ between subgroups; that question calls for a direct interaction analysis, which is not reported in the registry record.

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

• Overall Survival (OS) in the ITT Population
• Disease-free Rate at Year 3 in ITT Population
• Disease-free Rate at Year 3 in All Randomized Stage II-IIIA Population
• Disease-free Rate at Year 3 in PD-L1 (SP263 ≥ 1% TC) Subpopulation Within the Stage II-IIIA Population
• Disease-free Rate at Year 5 in ITT Population
• Disease-free Rate at Year 5 in All Randomized Stage II-IIIA Population
• Disease-free Rate at Year 5 in PD-L1 (SP263 ≥ 1% TC) Subpopulation Within the Stage II-IIIA Population
• DFS in the PD-L1 (SP263 ≥ 50% TC) Subpopulation Within the Stage II-IIIA Population

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time to the first of several events, rather than a simple count at a single visit. The registry defines disease-free survival as time from randomization to investigator-determined recurrence of non-small cell lung cancer, a new primary non-small cell lung cancer, or death, whichever came first. This combines clinically relevant events into one endpoint and gives each participant an event time or a period of event-free observation.

What does Kaplan-Meier estimation contribute?

In general, Kaplan-Meier estimation uses observed event times to estimate the probability of remaining event-free as follow-up proceeds. Participants who have no recorded event by their last observed time can still contribute information up to that point. Their later outcome is not treated as known. This approach is useful when follow-up duration varies, but interpretation depends on how censoring is defined and on whether censoring is sufficiently independent of the event process. The registry says Kaplan-Meier methods were used for the group medians; detailed censoring rules and checks are not reported in the registry record.

The median disease-free survival is the time at which the estimated event-free proportion reaches one half. It is a compact description of a time-to-event distribution, not a complete description of the curve. It does not say whether the groups differed consistently throughout follow-up, whether their curves crossed, or what happened after the median. The record gives median estimates and confidence limits, but the upper confidence limit for the atezolizumab median is not reported in the registry record.

How should the hazard ratio be understood?

The posted primary comparison is a hazard ratio for atezolizumab versus best supportive care, estimated using a log-rank method. In general, a hazard is an event rate among participants who have not yet experienced the event, at a particular point in follow-up. A hazard ratio compares those rates between groups. A value below 1 has a point-estimate direction toward a lower event rate in the first-named group under this convention; it is not a ratio of medians, and it is not a direct measure of the proportion of participants who avoid an event.

The reported hazard ratio is 0.848. Its 95% confidence interval is 0.710 to 1.013. Because the interval includes 1, the range of values compatible with the estimate includes no relative difference. The log-rank p-value is 0.068. The registry does not provide the primary test's decision threshold or a full analysis plan. It also does not report whether proportional hazards were assessed. In general, if relative hazards change over time, a single hazard ratio can be an incomplete summary of that pattern; the actual time pattern should be assessed from the event-time data and relevant diagnostics.

What does a confidence interval describe?

In general, a confidence interval expresses statistical uncertainty around an estimate under the method's assumptions. It is not a range guaranteed to contain the true value, nor does a confidence interval alone quantify the importance of an effect. The primary hazard-ratio interval extends across the null value of 1. The median intervals describe uncertainty in each group's median estimate separately; they are not themselves a direct interval for the difference between groups. The registry's reported primary comparison is the hazard ratio, rather than a confidence interval for the difference between medians.

Why can over-dispersion matter?

In general, over-dispersion arises when observed binary outcomes vary more than a statistical model expects. A model that assumes less variation than is present can produce confidence intervals that are too narrow and tests that are too optimistic. This concern is most relevant to models for counts or proportions when their assumptions do not fit the data. The primary endpoint is time-to-event, and the registry reports Kaplan-Meier estimation and a log-rank hazard ratio. It does not report an over-dispersion assessment. The Year 3 outcomes are proportions, but the posted record does not state that a particular over-dispersion model was used.

What is the role of the analysis population?

The primary intent-to-treat population is defined as all randomized participants with resected Stage IB tumors at least 4 centimetres through Stage IIIA disease, regardless of whether assigned treatment was received. In general, an intent-to-treat comparison retains participants in their randomized groups. That approach preserves the randomized allocation for the comparison and reflects assignment to the study strategies, rather than selecting only participants who completed treatment. It does not, by itself, resolve missing endpoint observations or explain how such observations were handled; those details are not reported in the registry record.

The trial was open-label, and the primary endpoint was assessed by the investigator. In general, knowledge of group assignment can affect decisions or assessments that involve judgment, even when an endpoint includes objective events. The registry does not report a blinded independent review for the primary outcome. Randomization addresses treatment allocation, but it does not remove every possible influence on outcome ascertainment or follow-up.

Finally, the primary analysis and the secondary analyses have different roles. The primary endpoint is the prespecified principal trial question as identified in the registry. Secondary endpoints can add context, but repeated testing across outcomes and populations increases the chance of apparently noteworthy findings arising by chance. The registry does not report a multiplicity-adjustment plan, so unadjusted secondary p-values and intervals should be treated as exploratory evidence rather than as independent confirmation of the primary result.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.848, with a 95% confidence interval from 0.710 to 1.013. The interval is relatively informative about the direction and scale of the estimate, but it still includes 1. Values on either side of 1 remain compatible with the reported interval. The p-value of 0.068 is another expression of uncertainty under the log-rank test; it does not remove the range of plausible effects indicated by the confidence interval.

The group medians are 65.6 months for atezolizumab and 47.8 months for best supportive care. For best supportive care, the reported median interval ranges from 37.0 to 65.8 months. For atezolizumab, the lower limit is 52.4 months, while an upper limit is not reported in the registry record. A missing limit should not be interpreted as an infinite interval or as evidence that the median is precisely known; it means the record does not give a complete two-sided interval for that estimate.

Confidence intervals for separate group medians do not directly answer the same question as a confidence interval for a treatment comparison. The hazard-ratio interval is the registry's direct comparative uncertainty estimate for the primary time-to-event analysis. In general, interval width depends on the amount of information available, including event occurrence and follow-up, as well as the analysis method. The registry reports the primary group sizes as 507 and 498, but does not provide the number of primary endpoint events or a detailed account of follow-up completeness. Those omissions limit a fuller assessment of precision.

Precision is not the same as clinical importance. A narrow interval can still cover effects of different practical importance, and a point estimate alone does not describe uncertainty. Here, the hazard-ratio interval includes the null value, while the median estimates have incomplete or broad uncertainty information. The posted data therefore support a cautious reading of the direction and magnitude of the estimates rather than a categorical conclusion.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on observed effects, not the original trial's sample-size justification. For time-to-event planning, the entries are total numbers of events. For the other outcomes, entries are participants per arm. Thus, the units differ across endpoint types and should be read from the accompanying label rather than treated as interchangeable measures of sample size.

The stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is a stated fraction of the observed effect. The time-to-event planning figures use the Schoenfeld approach and count total events; the other planning figures count participants per arm. The original design assumptions used to plan this trial are not reported in the registry record, so these illustrations should not be mistaken for the trial's own design calculation.

In plain language, the 80% power column gives the event or per-arm participant count estimated to provide an 80% chance of detecting the specified effect under the illustration's assumptions, if that effect and model are correct. The 90% power column represents a higher chance of detection under those same assumptions and therefore generally requires more information. Smaller assumed effects are harder to distinguish from random variation, so the planning illustrations require more events or participants when the assumed effect is reduced.

These figures are not observed power. Observed results and their confidence intervals are the appropriate basis for describing the trial's precision; a planning calculation cannot establish what the trial actually had power to detect after the outcome data were observed. Nor do these illustrations show that the trial enrolled the number needed for a particular effect, because they use the observed effect as their starting point rather than the unreported original design assumptions.

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 = 0.848, so ln(HR) = -0.1649.
2. d = 4 × (1.96 + 0.842)² / [ln(0.848)]² = 1,154.9, rounded up to 1,155 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 <- 0.848                              # 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(2486718)
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 = 1,155 (80% power), 1,547 (90% power)
 75% of observed effect: events = 2,054 (80% power), 2,749 (90% power)
 50% of observed effect: events = 4,620 (80% power), 6,185 (90% power)
Simulated power with 1,155 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 4,084 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 1,280 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 <- 47.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.848          # 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: 3974         p (1-sided)   0.0001
  Events: 522        ~HR at bound   0.7226
    Month: 23    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.85   0.0338
    IA 2: 67%                   Z   2.5114
      N: 4084         p (1-sided)   0.0060
 Events: 1044        ~HR at bound   0.8560
    Month: 38    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.85   0.5603
        Final                   Z   1.9930
      N: 4084         p (1-sided)   0.0231
 Events: 1566        ~HR at bound   0.9042
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.85   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 primary comparison reported by the registry is the sponsor's log-rank hazard ratio: 0.848, with a 95% confidence interval from 0.710 to 1.013 and p = 0.068. The posted primary comparison and the primary summary are consistent in their central estimate and interpretation. The interval includes 1, so uncertainty about the relative event rate remains.

For the Year 3 disease-free-rate outcomes, the registry also includes its own reported differences and confidence intervals. Simple unadjusted recalculations from the posted group summaries are descriptive checks, not replacements for the sponsor's analysis. The registry marks no discrepancy. Where an official sponsor analysis is reported, it is the authoritative result for describing that analysis; a recalculation based on summary data cannot reproduce adjustment choices, endpoint handling, or other details that are not available in the registry record.

The registry does not report complete statistical methods for every secondary analysis. Some reported sponsor results do not include a p-value in the record. Missing p-values should not be inferred from confidence intervals or recalculated summaries. The primary interpretation should therefore rely on the posted primary hazard ratio and its interval, while secondary recalculations are best treated as limited descriptive checks.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies disease-free survival in the intent-to-treat population as the primary outcome and lists several secondary outcomes, including overall survival, disease-free rates at Year 3 and Year 5, and outcomes in Stage II-IIIA and PD-L1-defined populations. Multiple outcomes and population subsets create a multiplicity issue: the more hypotheses examined, the greater the chance that at least one result will appear noteworthy by chance, even if there is no corresponding effect.

The registry record does not report whether secondary tests were adjusted for multiplicity, whether outcomes were tested in a fixed order, or whether some analyses were formally confirmatory and others exploratory. It also does not provide the full statistical analysis plan. As a result, unadjusted secondary estimates should not be read as if each were an isolated confirmatory test. Their role is to add context to the primary analysis, with appropriate caution.

The primary analysis population is defined as all randomized participants with resected Stage IB tumors at least 4 centimetres through Stage IIIA disease, regardless of receipt of assigned treatment. That is an explicit population definition, but it does not answer how missing or incomplete endpoint information was handled. The registry identifies Kaplan-Meier estimation, yet detailed censoring criteria, imputation methods, sensitivity analyses for missing outcomes, and the extent of missing primary endpoint data are not reported in the registry record.

The study was open-label and the primary endpoint was assessed by investigators. The record does not report a blinded independent endpoint review. These features matter for interpretation of recurrence assessment, especially because investigator judgment forms part of the endpoint definition. The registry also does not report a proportional-hazards assessment, detailed model diagnostics, or a complete account of the primary analysis assumptions. These omissions do not change the posted estimate, but they limit independent evaluation of how robust it is to alternative methods or assumptions.

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: febrile neutropenia (3.0%), pulmonary embolism (1.7%), pneumonia (1.6%), pyrexia (1.2%), neutropenia (1.0%).

The registry reports serious adverse events during the enrollment phase among 1269 participants at risk: 259 were recorded as affected, and 19 deaths were reported for that phase. After randomization, the best-supportive-care group had 42 affected among 495 at risk and 155 deaths; the atezolizumab group had 88 affected among 495 at risk and 154 deaths. These are descriptive counts in the registry record. They should be read with their stated group and phase, rather than combined or treated as rates with equal follow-up.

The listed leading serious adverse-event terms include febrile neutropenia at 3.0%, pulmonary embolism at 1.7%, pneumonia at 1.6%, pyrexia at 1.2%, neutropenia at 1.0%, and nausea at 0.9%. The record does not specify in this summary the denominator or exposure period for these term percentages, so they should not be converted into other measures or compared as if follow-up were identical.

Serious adverse-event counts and deaths alone do not establish whether an event was caused by treatment. The record excerpt does not give event-level timing, attribution, duration, or adjusted comparisons. The observed figures describe what was recorded in the registry; they do not, by themselves, support a causal interpretation of differences between groups.

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

The posted primary analysis estimates disease-free survival after resection and adjuvant cisplatin-based chemotherapy in the randomized intent-to-treat population. The median estimates and hazard-ratio point estimate favor atezolizumab in direction, while the hazard-ratio confidence interval includes 1. The results therefore contain both a directional estimate and material statistical uncertainty. The record does not justify turning the point estimate into a definitive statement about the effect for every participant or every setting.

The result applies to the study's defined population and treatment strategies: completely resected Stage IB-IIIA non-small cell lung cancer, following the enrollment-phase cisplatin-based chemotherapy, with randomization to planned atezolizumab or best supportive care. It does not directly answer questions about other cancer stages, unresected disease, different preceding treatments, or treatment strategies not studied in this comparison.

Disease-free survival combines recurrence, a new primary non-small cell lung cancer, and death. A difference in this composite endpoint does not identify which component accounts for the observed pattern. The registry record does not provide component-specific primary event results. Nor does the primary result alone establish an overall-survival difference; overall survival is listed as a secondary outcome, but its numerical result is not included in the registry entries described in this analysis.

The randomized design supports a comparison between assigned groups, but the study was open-label and the primary endpoint was investigator-assessed. The record does not report blinded independent review or detailed missing-data sensitivity analyses. Those considerations are relevant to how confidently the endpoint measurement and analysis can be evaluated. They do not erase the reported statistics, but they define limits on what can be concluded from them.

Finally, a statistical estimate is not a treatment recommendation. The record describes outcomes and uncertainty in a particular trial population; it does not determine what any individual should receive. Interpreting the result requires keeping the endpoint, population, comparator, analysis method, and limitations together rather than relying on a single number or a threshold-based label.

19. Why This Trial Matters Statistically

This trial illustrates why time-to-event results require more than a comparison of median values. The primary endpoint follows participants from randomization until recurrence, a new primary lung cancer, or death, and the registry uses Kaplan-Meier estimates for the medians. The comparative result is a hazard ratio with a confidence interval. Reading these summaries together makes clear that a point estimate can favor one group while the uncertainty interval still includes the null value.

It also illustrates the importance of separating the primary analysis from secondary analyses. The record lists multiple outcomes and populations, including disease-free rates at different years and in defined subgroups. Such analyses can add useful context, but their interpretation depends on whether they were prespecified, how tests were ordered, and whether multiplicity was addressed. Those details are not reported in the registry record, so secondary findings merit more restraint than the primary analysis.

The open-label design and investigator assessment are also statistically relevant. Randomization helps make the assigned groups comparable in expectation, but it cannot guarantee that outcome ascertainment is unaffected by knowledge of assignment. The endpoint includes recurrence as assessed by the investigator, and the record does not report independent blinded review. This makes transparent endpoint definitions and assessment procedures important parts of evaluating the result.

Finally, the planning illustrations based on the observed effect should not be confused with original trial design assumptions or observed power. The original sample-size justification is not reported in the registry record. Distinguishing a planning exercise from the actual randomized comparison prevents an illustrative calculation from being mistaken for evidence about the strength or validity of the trial's findings.

20. Limitations

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

The study was open-label, and disease-free survival was assessed by the investigator. The registry record does not report blinded independent review of recurrence events. Because recurrence assessment can involve judgment, lack of reported blinding limits how fully readers can evaluate the possibility of assessment differences between groups.

The record gives a primary hazard ratio and confidence interval but does not report whether the proportional-hazards assumption was assessed, how censoring was handled in detail, or what sensitivity analyses were conducted. It also does not report the number of primary endpoint events in the information. These omissions constrain independent assessment of the time-to-event analysis and the precision of the posted result.

The upper confidence limit for the atezolizumab median is not reported in the registry record. The record also does not provide numerical results for every listed secondary outcome in the registry record, including the listed overall-survival and Year 5 outcomes. A missing result should not be inferred from the available Year 3 estimates.

Multiplicity handling, the original sample-size justification, and interim-analysis plans are not reported in the registry record. The planning illustrations based on observed effects do not fill those gaps. The record also does not explain the relationship between the overall enrollment of 1280 and the primary endpoint group sizes of 507 and 498. The study's defined population is post-resection and post-chemotherapy, so the results should not automatically be extended to populations or treatment sequences outside that setting.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study to Assess Safety and Efficacy of Atezolizumab (MPDL3280A) Compared to Best Supportive Care Following Chemotherapy in Patients With Lung Cancer [IMpower010] — NCT02486718.
• Registry record last updated 2026-09-30; status last verified 2026-09.
• Results first posted 2025-03-30.
• 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

NCT02486718 is a completed Phase III randomized, open-label, parallel-group study sponsored by Hoffmann-La Roche. It enrolled 1280 participants and compared atezolizumab with best supportive care after resection and adjuvant cisplatin-based chemotherapy for Stage IB-IIIA non-small cell lung cancer.

The primary outcome was investigator-assessed disease-free survival in the intent-to-treat population, defined from randomization to recurrence, a new primary non-small cell lung cancer, or death. The reported median estimates were 65.6 months for atezolizumab and 47.8 months for best supportive care. The reported hazard ratio was 0.848, with a 95% confidence interval of 0.710 to 1.013 and p = 0.068.

The point estimate favors atezolizumab in direction, but the hazard-ratio interval includes 1. The registry record does not report the complete original design assumptions, multiplicity strategy, detailed missing-data handling, or all secondary-outcome results. The posted findings should therefore be interpreted with attention to their uncertainty, endpoint definition, and study population.