Chemotherapy in Treating Patients With Non-Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Chemotherapy in Treating Patients With Non-Small Cell Lung Cancer (NCT00520676), a randomized phase 3 study. The primary outcome is Survival Without Grade 3 or 4 Toxicity.

2. Clinical Question

The clinical question combines a toxicity event and death in a time-to-event outcome. A participant may therefore reach the endpoint through either a qualifying adverse event or death; the measure is not a toxicity-only count. Participants alive without Grade 3 or 4 toxicity were censored at their last contact, according to the registry description.

The trial also posted overall survival, progression-free survival, survival without clinically important Grade 3 or 4 toxicity, and other outcomes. These help describe what the primary comparison does and does not capture. In particular, the primary endpoint is not a general measure of all adverse effects, quality of life, tumor response, or survival considered separately.

3. Trial Design

The registry describes a randomized, Phase 3, parallel-group study with no masking. It compares pemetrexed plus carboplatin with docetaxel plus carboplatin as first-line treatment for patients with locally advanced or metastatic non-small cell lung cancer. The study status is completed. The record lists enrollment of 260 and gives the study start as 2007-10 and primary completion as 2010-07.

Both regimens used carboplatin AUC 5 intravenously every 21 days, for a maximum of 6 cycles. The pemetrexed regimen added pemetrexed 500 milligrams per square meter intravenously on the same schedule; the docetaxel regimen added docetaxel 75 mg/m^2 intravenously on that schedule. The registry lists Eli Lilly and Company as sponsor.

The primary outcome analysis used the protocol-qualified intent-to-treat population. The registry defines this group as randomized participants with nonsquamous histology who received at least 1 dose of study drug, analyzed according to assigned treatment. The posted primary arm counts are 106 for pemetrexed plus carboplatin and 105 for docetaxel plus carboplatin. The registry does not report a reconciliation of those analysis counts with the enrollment figure.

The primary endpoint was time from randomization to the first Grade 3 or 4 treatment-emergent adverse event or death due to any cause. The record describes a median, a 95% confidence interval, and a log-rank comparison with a reported hazard ratio. The stated observation timeframe was until 218 events, defined as death or Grade 3 or 4 toxicity, had been observed, up to 33.3 months. Details of additional design features, including the original sample-size justification and any interim analyses, 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: Analyses were conducted on the qualified intent-to-treat population (Q-ITT) unless otherwise specified. This population includes all data from all randomized participants, with nonsquamous histology, receiving at least 1 dose of the study drug according to the treatment the participants were assigned.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on protocol-qualified, intent-to-treat (Q-ITT) population. This population includes all data from all randomized participants, with nonsquamous histology, receiving at least 1 dose of the study drug according to the treatment the participants were assigned.

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 Survival Without Grade 3 or 4 Toxicity, measured over Baseline to until 218 events (defined as death or Grade 3 or 4 toxicity) have been observed (up to 33.3 months)..

The primary endpoint is the time from randomization to the first Grade 3 or 4 treatment-emergent adverse event or death from any cause. It combines a serious toxicity event with death, so it describes time until either event occurs rather than time to toxicity alone. The registry defines Grade 3 as severe or medically significant but not immediately life-threatening, with hospitalization or prolongation of hospitalization indicated. Grade 4 is described as life-threatening, with urgent intervention indicated. Severity grading used National Cancer Institute Common Terminology Criteria for Adverse Events, version 3.0.

The analysis reports the median time to the composite event for each regimen. A median is a time-to-event summary: it marks the point at which the estimated event-free proportion reaches the midpoint, subject to the survival-analysis methods and censoring. The record states that participants alive without Grade 3 or 4 toxicity were censored at their last contact. Censoring retains information up to the last known contact without treating that participant as having had the event at that time.

As a general statistical rationale, a time-to-event endpoint can use information about both whether an event occurred and when it occurred, while accommodating participants whose event time is not observed during follow-up. The composite outcome can provide a measure that includes both severe toxicity and death. Its interpretation remains tied to its components: a change in the composite does not by itself show which component accounts for the pattern. Component-specific contributions to the primary endpoint are not reported in the registry record.

7. Results Posted in the Registry

• Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin: hazard ratio 0.45 (95% CI 0.34–0.60), 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.

Overall Survival (OS)

• 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:
  • Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin: hazard ratio 1.01 (95% CI 0.72–1.42), reported p = 0.934 (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 Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin and the control. The interval gives the range of effects that remain compatible with the data.

Progression-free Survival (PFS)

• 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:
  • Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin: hazard ratio 0.96 (95% CI 0.72–1.29), reported p = 0.800 (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 Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin and the control. The interval gives the range of effects that remain compatible with the data.

Survival Without Clinically Important Grade 3 or 4 Toxicity

• 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:
  • Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin: hazard ratio 0.53 (95% CI 0.40–0.71), reported p < 0.001 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Pemetrexed Plus Carboplatin vs Docetaxel Plus Carboplatin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide context around the primary composite rather than a set of interchangeable tests of the same question. The registry posts overall survival, progression-free survival, tumor response, survival without clinically important Grade 3 or 4 toxicity, survival without Grade 4 toxicity, and adverse-event information. The posted time-to-event estimates show a broad pattern in which the primary composite and survival without clinically important toxicity have hazard-ratio estimates below 1, while the overall-survival and progression-free-survival comparisons do not show clear separation by their reported intervals and p-values.

This pattern is coherent in the limited sense that the toxicity-related time-to-event outcomes point in the direction of the primary result. It does not establish that the primary endpoint explains any difference in another outcome, nor does it establish that a result for one endpoint transfers to another. Overall survival, progression-free survival, tumor response, and toxicity summaries represent different outcomes and may have different event definitions and observation patterns. Results for the remaining secondary outcomes should be interpreted according to their own definitions.

Secondary results generally carry less weight than the designated primary result when many outcomes are examined. As a general statistical concern, repeated testing creates more opportunities for apparently notable findings even when no adjustment is made. The registry lists 6 secondary outcomes and 7 analyses, but a procedure controlling the overall false-positive rate is not reported in the registry record. It is therefore not appropriate to treat every secondary p-value as if it were an isolated, prespecified primary test.

Secondary findings can still be informative for describing the trial's outcome pattern and for identifying questions that warrant further study. Their interpretation should account for uncertainty, the absence of a reported multiplicity procedure, and the fact that the registry record does not report all analysis-plan details. The secondary outcomes should not be used to claim equivalence, prove benefit or harm on an unreported component, or override the endpoint definition used for the primary comparison.

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

• Overall Survival (OS)
• Progression-free Survival (PFS)
• Percentage of Participants With Tumor Response (Response Rate)
• Survival Without Clinically Important Grade 3 or 4 Toxicity
• Survival Without Grade 4 Toxicity
• Number of Participants With Adverse Events (AEs)

9. Statistical Interpretation

10. Statistical Methods Explained

Time-to-event analyses are used when the outcome includes the time until an event, and participants can have different lengths of observation. For the primary outcome, the event is the first Grade 3 or 4 treatment-emergent adverse event or death. The registry reports the median time for each treatment group and a log-rank comparison. These summaries answer related but different questions: the medians describe a point on each group's event-time distribution, while the hazard ratio summarizes the relative event rate over follow-up.

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

In general, a median survival estimate is the time at which the estimated probability of remaining free of the event reaches 50%. “Survival” in this statistical usage does not necessarily mean survival from death; it can refer to remaining free of any defined event. For this trial's primary endpoint, that means remaining alive without a Grade 3 or 4 treatment-emergent adverse event. The median should be interpreted with its confidence interval and the endpoint definition, not as a complete description of the event-time distribution.

The registry reports a median and 95% confidence interval for each primary arm. The time estimate does not state that all participants had an event by that point, nor does it describe the timing of every participant's event. The confidence interval reflects uncertainty in the estimated median. If the event-free curve does not cross its midpoint during observed follow-up, a median may not be estimable; that is not the situation conveyed by the posted primary arm estimates.

What does censoring contribute?

General explanation: censoring occurs when a participant's event time is not observed during the available follow-up. The registry says participants alive without Grade 3 or 4 toxicity were censored at their last contact. Their known event-free time contributes information until that contact; the censoring time is not treated as an event time. This approach depends on assumptions about the relationship between censoring and the chance of an event. The registry does not report diagnostic checks or further details about those assumptions.

For a composite that includes death, the interpretation of censoring must follow the stated endpoint definition. The registry describes censoring for participants alive without the qualifying toxicity. It does not provide additional detail on handling other circumstances that may affect follow-up or event ascertainment. Those details are not reported in the registry record.

How should the hazard ratio be read?

The reported primary hazard ratio is 0.45 for pemetrexed plus carboplatin versus docetaxel plus carboplatin. As a general explanation, a hazard ratio compares the event rates at a given time among participants who have not yet had the event. A value below 1 in this treatment ordering indicates a lower estimated event hazard in the first-named group relative to the comparator. It is not a risk ratio, an absolute risk reduction, or a subtraction of the median times. It also does not say that every participant has the same relative experience.

The registry reports the ratio as a log-rank analysis. A log-rank test compares the event-time experience between groups over follow-up while accounting for censoring. The reported p-value, p < 0.001, describes the compatibility of the observed comparison with a null hypothesis of no group difference under the test's assumptions. It is not the probability that the null hypothesis is true, nor a measure of the clinical importance of the result. Details of the statistical model used to estimate the hazard ratio beyond the reported method are not reported in the registry record.

General explanation: a single hazard ratio is easiest to summarize when the relative event rates are reasonably stable over time. If that relationship changes over follow-up, a single value can conceal time-varying patterns. The registry does not report an assessment of proportional hazards or other time-varying effects, so whether this issue was evaluated is not reported in the registry record.

What role do confidence intervals and p-values play?

A confidence interval gives a range of estimates compatible with the observed data under the analysis procedure. For the primary hazard ratio, the 95% interval is 0.34 to 0.60. Because the interval is entirely below 1, the estimated relative event hazard is lower for pemetrexed plus carboplatin across the interval of values shown. The interval does not include every uncertainty, such as uncertainty from unreported design choices, measurement, or selection of outcomes.

The p-value is a test statistic summarized as a probability under a specified null model. The reported p < 0.001 is evidence against the no-difference null in the primary log-rank comparison. It does not quantify the probability of a chance finding after accounting for all endpoints, because the registry does not report a multiplicity adjustment. A statistically small p-value also does not establish that an effect is clinically important.

What is and is not known about the analysis?

The registry identifies the primary population as protocol-qualified intent-to-treat: randomized participants with nonsquamous histology who received at least 1 dose, analyzed by assigned group. It reports the group counts and the outcome summaries. It does not report the original sample-size justification, the complete statistical analysis plan, interim analyses, or a multiplicity strategy. Missing-data handling beyond the stated censoring rule is not reported in the registry record.

These omissions matter because an analysis is interpreted in relation to the planned population, outcomes, and decision rules. The posted results can be described as recorded, while the absence of detail limits independent assessment of whether every analytic decision followed a prespecified plan. No inference about those unreported procedures should be made from the reported estimates alone.

11. Confidence Intervals and Precision

The primary median estimate was 3.2 months for pemetrexed plus carboplatin, with a 95% confidence interval from 2.1 to 3.7 months. For docetaxel plus carboplatin, the median was 0.7 months, with a 95% confidence interval from 0.5 to 1.2 months. These intervals describe uncertainty in each arm's median time-to-event estimate; they are not intervals for the difference between medians.

The primary relative comparison is reported as a hazard ratio of 0.45, with a 95% confidence interval from 0.34 to 0.60. The interval is below 1 throughout, so the set of values shown points in the same direction as the central estimate. The reported p-value is p < 0.001. A confidence interval gives a range of estimates compatible with the data under the specified procedure, rather than a range that contains a fixed proportion of individual participant outcomes.

Precision and statistical significance are related but not interchangeable. A narrow interval can indicate more precise estimation, while a small p-value addresses compatibility with a null comparison. Neither alone establishes the clinical importance of a result. The arm-specific median intervals and the hazard-ratio interval answer different questions and should not be compared as if they were the same statistic.

The registry reports 95% confidence intervals for these estimates, but it does not report additional precision diagnostics, such as the number of primary events within each arm or detailed follow-up distributions. The stated observation timeframe refers to 218 events for the study and up to 33.3 months; it does not provide a full account of the precision contribution from each event time. Interpretation should therefore remain with the posted estimates and their reported intervals.

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 the trial's original design justification. For time-to-event outcomes, the planning entries are total event counts, not participants per arm. Their meaning is therefore different from a participant-per-arm planning calculation. The primary endpoint illustration lists total-event targets for 80% and 90% power under each assumed fraction of the observed effect.

The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the treatment arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial design assumptions and sample-size justification are not reported in the registry record, so these illustrations should not be treated as the trial's planned target or as evidence about how its enrollment was chosen.

In plain language, the 80% power column describes the event target under which a study would have an 80% chance of detecting the assumed effect at the stated significance level, if that effect and the planning assumptions were correct. The 90% power column gives the corresponding target for a higher chance of detection under those same assumptions. These are prospective planning concepts; they do not describe the probability that this completed study detected an effect after its results are known.

The rows for planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect illustrate how the required event target changes when the assumed effect is smaller. Detecting a smaller effect generally requires more information, and these illustrations express that need as more total events for a time-to-event comparison. The 80% and 90% columns are not observed power. They are planning calculations based on an assumed effect and stated assumptions, not a retrospective score for the trial.

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 = 0.450, so ln(HR) = -0.7985.
2. d = 4 × (1.96 + 0.842)² / [ln(0.450)]² = 49.2, rounded up to 50 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 <- 0.45                              # 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(520676)
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 = 50 (80% power), 66 (90% power)
 75% of observed effect: events = 88 (80% power), 118 (90% power)
 50% of observed effect: events = 197 (80% power), 264 (90% power)
Simulated power with 50 events: 0.821 (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 68 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 260 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 <- 0.7          # control-arm median, months (converted from the posted unit)
hr          <- 0.45          # 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: 28         p (1-sided)   0.0001
 Events: 23        ~HR at bound   0.2070
  Month: 10    P(Cross) if HR=1   0.0001
            P(Cross) if HR=0.45   0.0338
  IA 2: 67%                   Z   2.5114
      N: 50         p (1-sided)   0.0060
 Events: 45        ~HR at bound   0.4706
  Month: 18    P(Cross) if HR=1   0.0060
            P(Cross) if HR=0.45   0.5603
      Final                   Z   1.9930
      N: 68         p (1-sided)   0.0231
 Events: 67        ~HR at bound   0.6136
  Month: 60    P(Cross) if HR=1   0.0250
            P(Cross) if HR=0.45   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 sponsor's reported primary analysis is a log-rank comparison with hazard ratio 0.45, 95% confidence interval 0.34 to 0.60, and p < 0.001. The posted result and the statistical reading use that reported analysis. The registry record indicates no discrepancy between the sponsor's analysis and the recalculated reading, so there is no competing estimate that needs to replace the sponsor's result.

Where a recalculation is labelled as such, it is a simple, unadjusted calculation from posted summary statistics. It does not reproduce a participant-level analysis and cannot account for information that is not present in those summaries. If the recalculation differed from the sponsor's own analysis, the sponsor's analysis would take precedence for describing the trial's reported result. That situation is not indicated for this record.

The sponsor-reported p-value and confidence interval should be read as inferential summaries of the specified log-rank comparison, not as a complete account of the analysis plan. Details such as the original sample-size justification, interim analyses, and multiplicity strategy are not reported in the registry record. Agreement between the reported analysis and an unadjusted calculation would not resolve those broader reporting gaps.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and also lists multiple secondary outcomes and analyses. Testing multiple outcomes can increase the chance of obtaining at least one small p-value even if the underlying effects are absent. Statistical approaches can address this by adjusting significance thresholds or otherwise controlling error across a family of tests. A multiplicity adjustment or a prespecified hierarchy for interpreting the outcomes is not reported in the registry record.

The absence of a reported adjustment does not change the numerical results, but it affects how strongly secondary findings should be treated as confirmatory. The primary comparison remains the clearest designated test in the registry description. Secondary comparisons are better read as supporting context unless a complete analysis plan establishes a different prespecified role. The record does not state whether any outcomes were selected or prioritized after examining the data.

The primary analysis population is described as protocol-qualified intent-to-treat, including randomized participants with nonsquamous histology who received at least 1 dose and analyzed according to assigned treatment. This definition is more specific than a population comprising all randomized participants. The posted primary arm counts are 106 and 105, while total enrollment is 260; the reason for the difference is not reported in the registry record. The record does not provide a participant-flow account that would explain exclusions or missing outcome information.

The registry specifies censoring at last contact for participants alive without Grade 3 or 4 toxicity. Other missing-data procedures, the extent of missingness, and sensitivity analyses are not reported in the registry record. The treatment of participants who withdrew, were lost to follow-up, or had incomplete assessments beyond the stated censoring rule is not described. These omissions limit assessment of how robust the findings are to missing information.

Interim analyses, stopping rules, the original statistical analysis plan, and the original sample-size justification are also not reported in the registry record. Those details cannot be inferred from the completed status or from the posted estimates. The record supports description of the stated population, outcomes, and reported analysis, but it does not support assumptions about unreported analytic decisions.

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: febrile neutropenia (8.6%), neutropenia (7.6%), pneumonia (6.7%), leukopenia (2.9%), atrial fibrillation (2.9%).

The registry reports serious adverse events affecting 28 participants in the pemetrexed plus carboplatin group and 35 in the docetaxel plus carboplatin group. The corresponding groups at risk are reported as 106 and 105. These are counts of participants with serious adverse events, not a severity-adjusted comparison or a time-to-event analysis. The registry also reports other adverse events affecting 94 and 100 participants in the respective groups, with the same group-specific at-risk counts.

The record lists febrile neutropenia at 8.6%, neutropenia at 7.6%, pneumonia at 6.7%, leukopenia at 2.9%, atrial fibrillation at 2.9%, and diarrhoea at 2.9% among the leading serious adverse-event terms. The registry listing does not establish from these term frequencies alone which regimen has a lower overall safety burden. The deaths field in the adverse-event summary is not reported in the registry record.

These summaries do not replace the primary endpoint. The primary measure includes Grade 3 or 4 treatment-emergent events and death over time, whereas the adverse-event summaries report counts of affected participants. Definitions, observation periods, and analysis populations matter when comparing the summaries. The record does not report a full event-level account or an adjusted statistical comparison for these safety counts.

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

The main statistical finding is that the sponsor-reported comparison of time to Grade 3 or 4 treatment-emergent toxicity or death has a hazard ratio below 1 for pemetrexed plus carboplatin relative to docetaxel plus carboplatin. Its 95% confidence interval is also below 1, and the reported p-value is p < 0.001. The arm-specific median estimates show the same direction for this defined composite. This is evidence of a difference in the posted primary time-to-event comparison under the reported analysis.

The result does not establish which part of the composite accounts for the observed comparison. The endpoint includes either Grade 3 or 4 toxicity or death, and component-specific primary results are not reported in the registry record. It also does not mean that every participant assigned to one regimen experiences a particular time to toxicity or death, or that the hazard ratio can be read as an absolute difference in the chance of an event.

The result is not a complete statement about overall survival, tumor response, or every type of adverse event. The secondary outcomes have their own estimates and uncertainty. In particular, the overall-survival and progression-free-survival comparisons do not show the same clear separation by their reported confidence intervals and p-values. A non-significant comparison does not establish that the treatments are equivalent; the registry does not report an equivalence or non-inferiority design with a prespecified margin.

The posted result also does not establish that the estimated difference is clinically important. Statistical evidence and clinical importance are distinct judgments, and the registry record does not report a threshold for a clinically meaningful change in this endpoint. The analysis applies to the stated protocol-qualified population and endpoint definition. It should not be extended beyond those conditions or treated as advice for an individual's care.

Finally, the registry record is not a complete account of every analytic choice. The original sample-size justification, interim analyses, multiplicity procedure, and additional missing-data methods are not reported in the registry record. Those gaps limit how fully the prespecification and robustness of the analyses can be assessed, without changing the fact that the posted primary result is statistically separated in the direction indicated by its hazard ratio.

19. Why This Trial Matters Statistically

This trial illustrates why an endpoint's definition is central to statistical interpretation. The primary outcome is not simply “toxicity” or “survival”: it is time to the first Grade 3 or 4 treatment-emergent adverse event or death. A hazard ratio for that composite answers a different question from a hazard ratio for death alone, and the primary result cannot identify which component drives the pattern when component-specific results are not reported.

It also demonstrates the complementary roles of medians, hazard ratios, confidence intervals, and p-values. The medians describe the timing of the composite event within each group. The hazard ratio compares event hazards between groups over follow-up. The confidence interval communicates uncertainty around the relative estimate, while the p-value assesses compatibility with a specified null comparison. None of these statistics substitutes for the others, and none alone describes every aspect of clinical importance.

The secondary outcomes show why outcome multiplicity matters. Different endpoints can display different patterns without contradiction because they measure different events. When many outcomes are analyzed, an unadjusted secondary p-value has a different evidential role from the designated primary test. The registry lists multiple outcomes but does not report a multiplicity strategy, making cautious separation of primary and secondary evidence especially important.

The planning illustrations also distinguish prospective sample-size reasoning from retrospective interpretation. They use observed effects and stated assumptions to illustrate event requirements; they do not show the trial's original design rationale or its observed power. Together, these features make the study useful for understanding how endpoint definitions, censoring, uncertainty, and multiplicity shape a clinical-trial result.

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 registry record does not report the component-specific results for the primary composite, so the relative contribution of Grade 3 or 4 toxicity and death cannot be assessed from the primary result alone. It also does not report detailed follow-up distributions, the number of events by arm, or an assessment of proportional hazards. These omissions limit evaluation of how well a single hazard ratio captures the event-time pattern.

The primary analysis population is restricted to randomized participants with nonsquamous histology who received at least 1 dose, analyzed by assigned treatment. The record does not explain the difference between the total enrollment of 260 and the posted arm analysis counts of 106 and 105. Without a participant-flow account, the reasons for that difference and the impact of exclusions cannot be assessed from the registry record.

Multiplicity control, interim analyses, the original sample-size justification, and the complete analysis plan are not reported in the registry record. Nor are additional missing-data methods or sensitivity analyses described beyond the censoring statement. These gaps make it harder to evaluate prespecification and the robustness of the findings, particularly for secondary outcomes.

The registry reports a limited set of adverse-event summaries, including counts of participants with serious and other adverse events and selected serious-event terms. The deaths field in that summary is not reported in the registry record. The record does not provide an adjusted comparison for the adverse-event counts, a comprehensive account of all event details, or a separate assessment of the primary composite components. These limitations constrain safety interpretation without changing the reported primary statistical comparison.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Chemotherapy in Treating Patients With Non-Small Cell Lung Cancer — NCT00520676.
• Registry record last updated 2011-08-10; status last verified 2011-08.
• Results first posted 2011-07-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

The registry describes a completed, randomized Phase 3 parallel-group study with no masking, comparing pemetrexed plus carboplatin with docetaxel plus carboplatin as first-line treatment for locally advanced or metastatic non-small cell lung cancer. Enrollment is listed as 260. The study start is 2007-10, and primary completion is 2010-07.

The primary endpoint was time from randomization to the first Grade 3 or 4 treatment-emergent adverse event or death. The sponsor-reported log-rank hazard ratio was 0.45, with a 95% confidence interval of 0.34 to 0.60 and p < 0.001. The primary analysis population was protocol-qualified intent-to-treat participants with nonsquamous histology who received at least 1 dose, analyzed as assigned.

The registry also reports secondary outcomes and adverse-event summaries. Multiplicity procedures, the original sample-size justification, interim analyses, and additional missing-data methods are not reported in the registry record. The posted evidence should be interpreted in relation to the composite endpoint, its analysis population, and the uncertainty and reporting limits.