A Study of Tarceva (Erlotinib) or Placebo in Combination With Platinum-Based Therapy as First Line Treatment in Patients With Advanced or Recurrent Non-Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Tarceva (Erlotinib) or Placebo in Combination With Platinum-Based Therapy as First Line Treatment in Patients With Advanced or Recurrent Non-Small Cell Lung Cancer (NCT00883779), a randomized phase 3 study. The primary outcome is Median Progression Free Survival (PFS) Time.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-blind, parallel-group phase III trial with two treatment groups. A total enrollment of 451 is listed. The primary outcome analysis includes the FAS population; the reported group sizes for that outcome are 225 for placebo and 226 for erlotinib. The record marks the study as completed.

Both groups received gemcitabine with platinum-based chemotherapy. The platinum agent could be cisplatin or carboplatin. The experimental group received erlotinib, while the comparison group received placebo. The registry summary describes treatment during six cycles followed by monotherapy, with study treatment anticipated to continue until disease progression. It describes gemcitabine on days 1 and 8, platinum chemotherapy on day 1, and erlotinib or placebo on days 15 to 28 of each four-week cycle. These are features described in the registry summary; more detailed operational protocol information is not reported in the registry record.

The primary outcome was median progression-free survival, assessed from randomization until progression or death. Tumor response assessments were scheduled at baseline and every eight weeks thereafter until progression, death or the end of the study, with the stated timeframe extending up to approximately 1.5 years. The record describes tumor evaluation using RECIST version 1.0 and Kaplan-Meier estimation for the primary outcome.

The registry record does not report the original sample-size justification, the trial's prespecified power assumptions, or whether interim analyses were planned or conducted. The existence of posted results does not by itself establish how those design decisions were made. Additional details about treatment adherence, protocol deviations and other operational features 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.

Primary Study Treatment Phase

Reasons for not completing this period:

Post-Study Treatment Phase

Reasons for not completing this period:

Off-study Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS population.

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: Full analysis set (FAS) population (Included all enrolled participants).

6. Primary Endpoint

The registry lists the primary outcome as Median Progression Free Survival (PFS) Time, measured over Randomization until PD or death (assessed at baseline and every 8 weeks thereafter until PD, death or end of study [up to approximately 1.5 years]).

Progression-free survival (PFS) is the time from randomization until the first documented disease progression or death from any cause, whichever occurs first. In this trial, progression was assessed using RECIST version 1.0. The registry description defines progression as an increase of at least 20% in the sum of the longest diameters of target lesions, using the smallest recorded sum since treatment began as the reference, or the appearance of one or more new lesions.

PFS is used in oncology trials because it captures the time participants remain alive without documented disease progression. It combines progression and death into one time-to-event outcome, rather than treating tumor response at a single assessment as the only measure. The primary result is summarized using Kaplan-Meier methods and median PFS, alongside a hazard ratio from a log-rank analysis.

Participants who had neither progressed nor died by the data cut-off, or who were lost to follow-up, were censored at the last assessment documenting non-progression or the last follow-up date for progression, whichever was later. Participants known to be alive but without a post-baseline tumor assessment were censored at randomization. Censoring allows a participant's observed time without an event to contribute information without treating the participant as having experienced progression or death. Its interpretation depends on the follow-up and censoring process; the registry description does not provide further detail about how that assumption was evaluated.

7. Results Posted in the Registry

• Placebo vs Erlotinib: hazard ratio 0.57 (95% CI 0.46–0.70), 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.

Percentage of Participants Alive and Free From Disease Progression

• 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:
  • Erlotinib: 22.6% (51/226) versus 6.2% (14/225) on control; risk difference 16.3 percentage points (95% CI 10.0 to 22.6), risk ratio 3.63 (2.07–6.36); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Erlotinib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Non-Progression Rate: Percentage of Participants With a Confirmed Best Overall Response of Either Complete Response (CR) or Partial Response (PR) or Stable Disease (SD) for At Least 16 Weeks

• 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:
  • Erlotinib: 67.3% (152/226) versus 64.4% (145/225) on control; risk difference 2.8 percentage points (95% CI -5.9 to 11.6), risk ratio 1.04 (0.91–1.19); unadjusted two-proportion z-test p = 0.529.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Erlotinib and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate: Percentage of Participants With a Confirmed Best Overall Response of CR or PR

• 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:
  • Erlotinib: 42.9% (97/226) versus 17.8% (40/225) on control; risk difference 25.1 percentage points (95% CI 17.0 to 33.3), risk ratio 2.41 (1.76–3.32); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Erlotinib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several related but distinct aspects of disease course: being alive without progression, the duration of overall survival, response, non-progression, duration of response and time to progression. The registry also lists subgroup analyses for some outcomes. Taken together, these outcomes can provide context for the primary PFS result, but they do not all measure the same construct or use the same statistical approach.

At a broad level, the posted results include a more clearly separated objective-response finding, while the non-progression-rate comparison is less distinct. This pattern shows why secondary outcomes should be interpreted individually rather than treated as a single body of interchangeable evidence. A higher response proportion can coexist with a different pattern for a broader disease-control definition, and neither alone establishes the full time course of progression-free survival.

The registry lists 16 outcome measures and 34 analyses. In general, when many outcomes and subgroup comparisons are examined, the chance of at least one apparently notable result arising by chance can increase unless an analysis plan addresses multiplicity. The record does not report whether adjustments or a hierarchical testing strategy were prespecified. Unadjusted secondary p-values therefore carry less weight than a single prespecified primary analysis, especially when the full multiplicity plan is unavailable.

Secondary outcomes are still useful for describing the trial and generating questions for further study. Their interpretation should consider whether the endpoint was prespecified, how it was measured, the size and precision of the estimate, and whether the analysis accounts for the number of comparisons. The registry record does not report enough detail to resolve all of those considerations. These results should be viewed as supporting context rather than independent proof of the primary finding.

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

• Percentage of Participants Alive and Free From Disease Progression
• Median PFS Time Based on Different Subgroups
• Median Overall Survival (OS) Time-Overall and Among Different Subgroups
• Percentage of Participants Alive at the End of Study-Overall and Among Different Subgroups
• Non-Progression Rate: Percentage of Participants With a Confirmed Best Overall Response of Either Complete Response (CR) or Partial Response (PR) or Stable Disease (SD) for At Least 16 Weeks
• Objective Response Rate: Percentage of Participants With a Confirmed Best Overall Response of CR or PR
• Duration of Response
• Time to Progression

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. In general, time-to-event methods are useful when participants are followed for different lengths of time or some participants have not experienced the event by the end of observation. Rather than treating those participants as if they had an event, the analysis uses their observed event-free follow-up up to the point at which their status is censored. The registry description specifies the censoring rules used for PFS, including the last assessment documenting non-progression for participants without a recorded event.

The primary analysis used the Kaplan-Meier method. In general, a Kaplan-Meier curve estimates the proportion of participants who remain free of the event over follow-up, accounting for censoring. The median is the time at which the estimated curve reaches one half. A median is a useful summary, but it does not show the full shape of the curve or how estimates change across follow-up. Nor does comparing medians alone use all the timing information in the same way as a time-to-event comparison.

The registry reports a hazard ratio and a log-rank method for the primary comparison. In general, a hazard ratio compares the instantaneous event rates between groups over follow-up, conditional on participants having remained event-free up to each time. It is not a direct comparison of median times, and it should be interpreted in the context of the event definition, follow-up and analysis. The log-rank test compares the observed and expected event patterns between groups over time. The registry provides the hazard ratio, confidence interval and p-value, but further details of the statistical model or of any checks of its assumptions are not reported in the registry record.

A p-value describes how compatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The reported primary p-value is less than < 0.001. The confidence interval is useful alongside it because the interval conveys a range of estimates compatible with the data and analysis, rather than reducing the result to a threshold decision.

For binary outcomes, a percentage describes the share of participants meeting the outcome definition in each group. The secondary analyses include comparisons of such outcomes. A risk difference expresses the difference between the observed proportions in the groups; a confidence interval around that difference describes uncertainty in the estimated difference. General interpretation should account for the event definition and the amount of information in each group. The registry record also reports sponsor analyses for some secondary outcomes using chi-squared methods.

For time-to-event planning illustrations, the record gives total event counts rather than participants per arm. The stated planning approach uses the Schoenfeld method. In general, event-driven planning for a time-to-event comparison focuses on how many outcome events are needed to estimate a contrast, because events supply information about the relative event pattern. Other planning illustrations are expressed as participants per arm and use a normal approximation for a two-group comparison. The posted planning assumptions are two-sided significance level 0.05 and equal allocation between groups, with the effect to detect set to the stated fraction of the observed effect.

Over-dispersion is a general concern when the variability in data is greater than a model assumes; it can make standard errors too small if ignored. The primary outcome is time-to-event, and the registry record does not describe an over-dispersion adjustment. This concept should not be taken to imply that over-dispersion was present in this trial. More broadly, a statistical method is only as informative as its outcome definitions, follow-up and assumptions.

The registry identifies the FAS population for the primary outcome. It does not explain in the information how that population was defined, whether all randomized participants were included, or how protocol deviations were handled. Further statistical details, including the handling of multiplicity and any planned interim analyses, are not reported in the registry record. General explanations of statistical methods do not fill in those trial-specific omissions.

11. Confidence Intervals and Precision

The primary PFS medians are 6.0 months for placebo, with a 95% confidence interval of 6.0 to 7.0 months, and 7.6 months for erlotinib, with a 95% confidence interval of 7.0 to 8.0 months. The sponsor-reported hazard ratio is 0.57, with a 95% confidence interval of 0.46 to 0.70. These intervals describe uncertainty in distinct estimates: the median intervals relate to each group's median, while the hazard-ratio interval relates to the relative time-to-event comparison. They should not be treated as if they answer the same question.

In general, a confidence interval gives a range of values reasonably compatible with the observed data under the method's assumptions. It is not a guarantee that the true value lies within the interval, and its width is informative about precision. A narrower interval indicates more precision for the parameter being estimated, while a wider interval indicates greater uncertainty. The interval does not account for every possible source of bias, such as limitations in outcome measurement or follow-up.

The reported hazard-ratio interval lies below 1, and the registry reports p < 0.001 for the log-rank analysis. Together, these quantify the statistical evidence and uncertainty for the primary comparison as analyzed. They do not by themselves determine the clinical importance of the result. That assessment depends on the outcome, the treatment context, potential harms and the priorities relevant to interpreting the trial.

Some secondary outcomes have confidence intervals, while others do not have intervals posted in the registry results. The absence of an interval for a particular result should not be read as evidence of certainty. The precision of secondary estimates also varies with the number of participants and events contributing to each outcome. The registry record does not report confidence intervals for every secondary measure.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are based on the observed effect and are not a report of the trial's original design calculation. For time-to-event planning, each figure is the total number of events required across groups, not a number of participants per arm. For the other outcomes, figures are participants per arm. The stated 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 the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld method.

The 80% power column gives the number of events or participants needed under those assumptions for an 80% chance of detecting the specified effect if that effect were the true effect and the assumptions held. The 90% power column gives the corresponding planning quantity for a 90% chance. These are design-planning concepts, not guarantees about a future study's result. The illustrations do not identify the trial's original power target or its original sample-size rationale; those are not reported in the registry record.

Rows that plan for 75% or 50% of the observed effect consider smaller effects than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more events or participants under the same planning assumptions. The figures are illustrative because the observed effect can be imprecise and may not be the effect a future study would experience.

This is not observed power. Observed power is not a useful substitute for interpreting the confidence interval and the results actually recorded. The planning figures answer a hypothetical design question: what event count or group size would be needed under specified assumptions for a stated effect and target power?

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 = 0.570, so ln(HR) = -0.5621.
2. d = 4 × (1.96 + 0.842)² / [ln(0.570)]² = 99.4, rounded up to 100 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 <- 0.57                              # 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(883779)
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 = 100 (80% power), 134 (90% power)
 75% of observed effect: events = 177 (80% power), 237 (90% power)
 50% of observed effect: events = 398 (80% power), 533 (90% power)
Simulated power with 100 events: 0.810 (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 152 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 451 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 <- 6          # control-arm median, months (converted from the posted unit)
hr          <- 0.57          # 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: 102         p (1-sided)   0.0001
  Events: 45        ~HR at bound   0.3289
   Month: 16    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.57   0.0338
   IA 2: 67%                   Z   2.5114
      N: 152         p (1-sided)   0.0060
  Events: 90        ~HR at bound   0.5873
   Month: 25    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.57   0.5603
       Final                   Z   1.9930
      N: 152         p (1-sided)   0.0231
 Events: 134        ~HR at bound   0.7083
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.57   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 PFS comparison, the registry reports the sponsor's own hazard-ratio analysis: 0.57, with a 95% confidence interval of 0.46 to 0.70 and p < 0.001, using a log-rank method. The primary time-to-event result is presented using that reported estimate. A separate unadjusted re-calculation is not used for this outcome; the registry record identifies the sponsor's reported hazard ratio as the basis for the primary comparison.

For some secondary binary outcomes, the posted results include sponsor analyses as well as simple unadjusted re-calculations from the displayed group summaries. Those calculations can differ slightly because the methods or rounding may not be identical. They are descriptive checks, not replacements for the trial's own analysis. The sponsor's analysis should be distinguished from any simple calculation based on group-level counts and percentages.

The registry record does not give enough detail to reconstruct every part of the sponsor's statistical implementation, such as all model specifications or assumptions. Accordingly, the sponsor-reported estimate and its stated method should be read as the trial's reported analysis, while any unadjusted recalculation is best understood as a secondary arithmetic perspective rather than an independent validation of the full analysis.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study conducts many statistical tests. In general, the more comparisons made, the greater the chance that at least one result will appear statistically notable even if there is no underlying effect for that comparison. Methods such as prespecified outcome hierarchies or adjustments to significance thresholds can address this issue, but the registry record does not report whether such methods were planned or used.

The record lists 16 outcome measures and 34 analyses, including outcomes and subgroup analyses. This makes the missing multiplicity information relevant when interpreting secondary p-values. The primary PFS outcome is identified, and its reported analysis uses a log-rank method; however, the registry information does not state how the primary test related to any broader family of planned tests.

For the primary outcome, the registry specifies a FAS population and describes censoring for participants without a recorded progression or death during observation. Participants with no post-baseline tumor assessment who were known to be alive were censored at randomization. The record does not further describe how missing assessments, treatment discontinuation, protocol deviations or missing data in secondary outcomes were handled. These details are not reported in the registry record.

The registry gives a PFS assessment schedule and a stated follow-up timeframe, but it does not provide a full account of participant-level follow-up completeness or the reasons for missing assessments. Censoring is part of the stated time-to-event analysis; it does not remove the need to consider whether incomplete observation could affect interpretation. Further information about sensitivity analyses for censoring or missing data is not reported in the registry record.

The record also does not report the original sample-size justification, the complete prespecified statistical analysis plan, or whether interim analyses were planned or conducted. These omissions limit the ability to assess the trial's design choices and the context for all reported analyses. They do not alter the numerical results posted, but they constrain how fully the analysis process can be evaluated.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: anaemia (11.7%), thrombocytopenia (7.2%), pneumonia (4.1%), dyspnoea (2.7%), neutropenia (1.8%).

The registry reports serious adverse events affecting 76 of 222 participants at risk in the placebo group and 70 of 226 participants at risk in the erlotinib group. These are serious-event counts, not counts of all adverse events, and the denominators differ from the primary outcome group sizes. The record also lists serious adverse event terms, including anaemia, thrombocytopenia and pneumonia, with percentages. The listed terms should not be interpreted as a complete account of all safety outcomes.

These figures describe events recorded in the registry and should not be read as proof that a treatment caused an event. A comparison of counts alone does not capture timing, severity beyond the serious-event classification, duration, recurrence or the clinical circumstances of each event. The registry record does not provide the information needed to characterize those details fully.

Death counts are not reported in the adverse-event information. The registry record also does not provide a full narrative of adverse-event ascertainment or a complete treatment-relatedness analysis in this summary. Safety interpretation therefore requires attention to the definitions, follow-up and reporting context, alongside the efficacy results.

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

The primary result shows that the registry's reported PFS analysis found a difference between the randomized groups. The median estimates and hazard ratio describe that difference in different ways: the medians summarize each group's estimated time-to-event distribution, while the hazard ratio summarizes a relative event-rate comparison over follow-up. The confidence interval and p-value quantify statistical uncertainty and evidence under the stated analysis.

These results do not establish how an individual participant will fare. A group-level median is not a predicted personal outcome, and a hazard ratio is not a direct measure of the amount of time gained by every participant. The estimates also do not by themselves establish whether the size of the difference is clinically important. That judgment depends on the broader treatment context, potential harms, participant priorities and other evidence beyond the primary statistical comparison.

The trial compared erlotinib with placebo when each was used alongside gemcitabine and platinum-based chemotherapy in the studied population. It does not isolate the effect of erlotinib from every other aspect of care in settings that differ from the trial. Generalization to other disease groups, treatment combinations or clinical settings requires evidence that those populations and circumstances are sufficiently comparable.

Secondary endpoints add context but do not erase the distinctions between outcomes. Response, non-progression, survival and time-to-event endpoints measure different features, and numerous analyses make unadjusted secondary findings less definitive. Safety counts also require separate interpretation and should not be reduced to a single comparison of totals.

The registry record does not report the full original design rationale, multiplicity strategy, interim-analysis plan or all missing-data procedures. Those gaps limit assessment of the analysis plan and the robustness of every secondary finding. They do not justify assuming that an unreported procedure was or was not performed. The most grounded interpretation is the one tied to the posted primary analysis, its confidence interval and its stated endpoint definition.

19. Why This Trial Matters Statistically

This trial illustrates why time-to-event results should be interpreted using more than a pair of medians. The primary endpoint combines progression and death and uses follow-up information from participants who did not experience a recorded event before censoring. Kaplan-Meier estimates, medians and a hazard ratio each describe different aspects of that outcome. Keeping those quantities distinct helps avoid treating the hazard ratio as a ratio of median times or treating a median as a complete description of follow-up.

It also shows the value of reading uncertainty alongside a point estimate. The reported hazard ratio is accompanied by a confidence interval and a log-rank p-value. Those statistics offer complementary information: one gives an estimate, one conveys precision, and one quantifies compatibility with a null comparison under the analysis. None alone answers every question about clinical importance or generalizability.

The many secondary measures make multiplicity a practical interpretive issue. A broad endpoint set can describe response and disease course from several angles, but the number of analyses raises the importance of knowing whether a testing strategy was prespecified. Because that strategy is not reported in the registry record, secondary results warrant more cautious interpretation than the designated primary comparison.

Finally, the record distinguishes trial results from hypothetical sample-size planning. Planning illustrations based on observed effects can help explain how assumptions about effect size and power affect required information, but they cannot reveal the original design rationale or the power achieved in the completed trial. Together, these features make the study useful for understanding both the strengths of randomized time-to-event evidence and the limits imposed by incomplete reporting.

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 trial-specific limitations affect how completely the registry results can be assessed. The registry record does not report the original sample-size justification, the prespecified statistical analysis plan in full, or whether interim analyses were planned or conducted. Without that information, it is not possible to evaluate the design rationale or the intended relationship among primary, secondary and subgroup tests.

The record lists numerous outcome measures and analyses but does not report a multiplicity strategy. This matters most when interpreting secondary findings, where repeated testing can make isolated p-values less reliable as confirmatory evidence. The record also does not provide full detail about missing assessments or sensitivity analyses for the PFS censoring process. Although the primary endpoint description specifies censoring rules, it does not establish whether censoring was unrelated to future outcome in the way required for straightforward interpretation.

The primary outcome is identified for the FAS population, but the information does not define that population in detail or explain how protocol deviations and incomplete follow-up were handled. Secondary outcome analyses may also have different available denominators, and the registry summary does not provide a complete account of missingness for each endpoint.

Safety information is limited to the reported serious-event counts and listed terms in this summary. Death counts are not reported in the adverse-event information, and the record does not give a full account of event timing, treatment relatedness or other safety details. These limitations do not invalidate the posted findings, but they restrict the conclusions that can be drawn from the registry record alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Tarceva (Erlotinib) or Placebo in Combination With Platinum-Based Therapy as First Line Treatment in Patients With Advanced or Recurrent Non-Small Cell Lung Cancer — NCT00883779.
• Registry record last updated 2015-12-14; status last verified 2015-11.
• Results first posted 2015-12-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

The registry describes a completed randomized, double-blind, parallel-group phase III study of erlotinib or placebo with gemcitabine and platinum-based chemotherapy as first-line treatment for advanced or recurrent non-small cell lung cancer. Total enrollment was 451. The primary outcome was median PFS, measured from randomization to progression or death.

The posted primary analysis reports median PFS of 6.0 months for placebo and 7.6 months for erlotinib. The reported hazard ratio is 0.57, with a 95% confidence interval of 0.46 to 0.70 and p < 0.001 using a log-rank method. Secondary outcomes cover progression, response, survival and safety, but their interpretation is limited by unreported multiplicity and other analysis-plan details.

The registry record provides endpoint definitions and some censoring information, but the original sample-size rationale, full statistical plan, interim-analysis information and further missing-data procedures are not reported in the registry record.