Maintenance Chemotherapy With or Without Local Consolidative Therapy in Treating Patients With Stage IV Non-small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Maintenance Chemotherapy With or Without Local Consolidative Therapy in Treating Patients With Stage IV Non-small Cell Lung Cancer (NCT03137771), a randomized phase 2 study. The primary outcome is [Phase II] Progression-free Survival.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. Its listed phase is phase II, while the official title describes a randomized phase II/III trial. The stated enrollment is 218. The trial concerns maintenance chemotherapy with or without local consolidative therapy for patients with stage IV non-small cell lung cancer, and the official title specifies limited metastatic non-small cell lung cancer.

One group received systemic maintenance chemotherapy. The other group received local consolidative therapy in addition to systemic maintenance chemotherapy. Local consolidative treatment was described as radiation to the primary tumor and metastatic sites or surgery of metastatic sites. Radiation options listed in the record include stereotactic body radiation therapy, hypofractionated radiation using intensity-modulated radiation therapy or three-dimensional conformal radiation therapy, and other radiation approaches. The maintenance therapies listed include docetaxel, pemetrexed, erlotinib, gemcitabine, and pembrolizumab. The registry’s arm descriptions include conditional treatment options rather than one identical regimen for everyone.

The trial record gives a start date of 2017-04-07 and a primary completion date of 2023-12-20. Its current status is active, not recruiting. The primary endpoint is identified as phase II progression-free survival. The modified intent-to-treat population includes randomized eligible participants. The endpoint description says the analysis was to occur after progression or death had been reported for 138 participants, and gives a maximum follow-up time at analysis of 5.4 years.

These design details define the context for interpreting the posted comparison. Randomization supports a comparison between assigned treatment strategies, but the registry record does not describe the allocation procedure beyond stating that allocation was randomized. It does not report masking, because masking is listed as none. The record’s treatment descriptions should be read as strategy-level descriptions: systemic treatment choices and local treatment modalities could vary, so the result does not isolate the effect of one particular drug or radiation technique.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat population (randomized eligible participants).

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: Modified intent-to-treat population (randomized and eligible).

6. Primary Endpoint

The registry lists the primary outcome as [Phase II] Progression-free Survival, measured over From randomization to first date of local or regional disease, distant metastases, second primary tumor, death, or last follow-up, whichever comes first. Maximum follow-up time at time of analysis was 5.4 years..

Progression-free survival measures the time from randomization until the first qualifying event. The registry defines these events as local or regional disease, distant metastases, a second primary tumor, or death due to any cause. If a participant has no recorded event by the last known follow-up, that time is censored rather than treated as an event.

This endpoint is useful in a trial comparing strategies intended to control cancer because it captures the time until a broad set of disease or survival events, rather than relying on a single type of progression. Including death from any cause means that death contributes to the endpoint even when the record does not identify cancer progression first. The composite definition also means that the result does not separately tell how long participants remained free of each individual event type.

The primary measure is the median progression-free survival estimated by the Kaplan-Meier method. A median is the estimated time by which half of the population has experienced the endpoint event, accounting for censoring. It is not an arithmetic average of observed follow-up times. The registry also reports a hazard ratio from a log-rank comparison. That relative measure uses event-time information across follow-up and complements, rather than replaces, the medians.

Progression-free survival is not the same as overall survival, and the primary result should not be read as a direct measure of quality of life or of any one treatment’s effect on a particular disease event. Those questions require separate outcomes and analyses.

7. Results Posted in the Registry

• Arm 1 (Systemic Maintenance Chemotherapy) vs Arm 2 (LCT + Systemic Maintenance Chemotherapy): hazard ratio 0.98 (95% CI 0.68–1.40), reported p = 0.660 (as reported in the registry).

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is a time-to-event outcome. Each participant’s time begins at randomization and ends at the first qualifying progression-free-survival event, or at the last known follow-up if no event has been recorded. The registry specifies local or regional disease, distant metastases, a second primary tumor, and death due to any cause as events. A participant whose follow-up ends before a recorded event contributes information up to the last known follow-up and is censored at that point.

What does Kaplan-Meier estimation do?

In general, the Kaplan-Meier method estimates the probability of remaining free of an event over time while accounting for censoring. It does not require every participant to have an observed event. Participants who are censored contribute information while they are followed, but their later event status is unknown. The method produces an estimated event-free survival curve; the median is the time at which that estimated curve reaches the halfway point. The registry identifies Kaplan-Meier estimation for the progression-free survival medians.

A median from this method is not the mean follow-up time and is not an average of individual event times. It is a summary of the estimated distribution of time to the defined endpoint. When many participants are censored or the curve is imprecisely estimated, the median and its confidence interval can be uncertain. Here the registry reports a 95% confidence interval for each group’s median. Those intervals should accompany the point estimates when describing the result.

How should the hazard ratio be understood?

In general, a hazard is the instantaneous rate of experiencing an event among participants who have not yet experienced it, as follow-up proceeds. A hazard ratio compares the hazards between groups. A value near 1 represents similar estimated hazards in the comparison; values on either side of 1 indicate different relative directions, depending on the order of the groups in the comparison. A hazard ratio is not a ratio of median survival times, and it does not directly state the proportion of participants who will experience an event.

The registry reports a hazard ratio of 0.98 and a 95% confidence interval of 0.68 to 1.40. It identifies the statistical method as log rank. The record does not give further detail about the estimation procedure for the hazard ratio or report an assessment of the assumptions used to interpret it. The value should therefore be read as the sponsor-reported relative time-to-event estimate, with its confidence interval, rather than as a complete description of the underlying event-time patterns.

What does the log-rank test contribute?

In general, the log-rank test compares event-time experience between groups while taking account of when events occur and when participants are censored. It tests whether the observed time-to-event patterns differ more than would be expected under a null comparison. The registry reports a log-rank p-value of 0.66. A p-value measures how compatible the observed data are with that null comparison under the test; it is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

The log-rank p-value and the confidence interval serve different interpretive purposes. The p-value summarizes evidence against the null under the test, while the interval shows a range of relative effect estimates compatible with the data and the interval procedure. The interval is especially useful for seeing that the observed estimate does not pin down a single effect precisely. Neither measure alone proves that a difference is absent.

Why can censoring and over-dispersion matter?

In general, censoring is expected in time-to-event research because participants may reach the end of follow-up without an event or may have no later event information available. Censoring is not itself an event. Kaplan-Meier and log-rank methods can use censored observations, but their interpretation depends on adequate follow-up and appropriate handling of censoring. The registry defines last known follow-up as the censoring time for the primary outcome. More detailed descriptions of censoring patterns and missing follow-up are not reported in the registry record.

Over-dispersion is a general concern when a statistical model for counts or rates assumes less variability than the data actually contain. It can lead to uncertainty being understated if the model does not accommodate the extra variation. The primary endpoint is time-to-event rather than a simple count outcome, and the registry identifies Kaplan-Meier estimation and a log-rank comparison. It does not report an over-dispersion adjustment. This general issue should not be mistaken for a method reported for this analysis.

There are multiple secondary outcomes in the registry, including local failure, new lesions, adverse events, and duration of maintenance chemotherapy. When several outcomes or comparisons are examined, multiplicity can affect the chance of at least one apparently notable finding. The record lists four secondary outcomes but does not report a multiplicity adjustment or a hierarchy for interpreting them. The primary progression-free survival result should therefore be kept distinct from any secondary findings.

Finally, the registry says that analysis was to occur after progression or death had been reported for 138 participants. It also states that the maximum follow-up time at analysis was 5.4 years. These are features of the specified analysis context, not a complete account of monitoring or data handling. Interim analyses and the trial’s original statistical plan are not reported in the registry record.

10. Confidence Intervals and Precision

The progression-free survival medians are 11.1 months for systemic maintenance chemotherapy and 13.7 months for local consolidative therapy plus systemic maintenance chemotherapy. Their 95% confidence intervals are 6.9 to 21.4 months and 8.6 to 20.1 months, respectively. These intervals communicate uncertainty in the estimated medians. They are not ranges containing a fixed proportion of individual participants’ survival times.

The relative comparison is reported as a hazard ratio of 0.98, with a 95% confidence interval from 0.68 to 1.40. In general, a confidence interval represents a range of estimates compatible with the observed data under the method’s assumptions. It conveys precision as well as direction: a narrower interval would indicate more precise estimation, while a wider interval allows a broader range of possible effects. The interval includes relative hazard values both below and above 1, so it does not precisely establish the direction or size of a difference.

The p-value of 0.66 is consistent with limited evidence against the null comparison in the log-rank test. It should not be interpreted as a probability that there is no treatment effect. Nor does the interval prove that effects within its bounds are equally plausible or clinically interchangeable. The registry does not report a margin for equivalence or noninferiority.

Precision depends on the amount and distribution of event-time information, follow-up, and censoring, among other features. The record gives the analysis population, a planned event threshold, and maximum follow-up time at analysis, but does not report detailed censoring patterns or the uncertainty associated with every subgroup or secondary outcome. The confidence intervals are therefore central to interpreting how much can be concluded from the primary result.

11. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. Because this is a time-to-event analysis, the entries are total numbers of events, not participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

The 80% power column gives the total event count that the planning calculation associates with an 80% chance of detecting the chosen effect under those assumptions, if that effect is real. The 90% power column gives the corresponding event count for a higher chance of detection. These are prospective planning quantities, not counts of participants observed in this trial, and they are not observed power.

For planning at 100% of the observed effect, The table shows 76,922 total events for 80% power and 102,977 for 90% power. For planning at 75% of the observed effect, it lists 136,750 and 183,069 total events. For planning at 50% of the observed effect, it lists 307,687 and 411,905 total events. The curve should be read in the same way: it illustrates how the required event information changes as the target effect changes, under the stated planning assumptions.

Smaller effects are harder to distinguish from random variation, so they require more event information to reach the same planned power. The very large event requirements in these illustrations follow from using the observed hazard-ratio estimate as the basis for planning and should not be read as evidence about how many events this trial actually recorded. The registry’s original sample-size justification and design assumptions are not reported in the registry record.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.980, so ln(HR) = -0.0202.
2. d = 4 × (1.96 + 0.842)² / [ln(0.980)]² = 76,921.6, rounded up to 76,922 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 <- 0.98                              # 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(3137771)
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 = 76,922 (80% power), 102,977 (90% power)
 75% of observed effect: events = 136,750 (80% power), 183,069 (90% power)
 50% of observed effect: events = 307,687 (80% power), 411,905 (90% power)
Simulated power with 76,922 events: 0.802 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

13. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 125,557 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 218 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 <- 11.1          # control-arm median, months (converted from the posted unit)
hr          <- 0.98          # 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: 92822         p (1-sided)   0.0001
  Events: 34731        ~HR at bound   0.9610
      Month: 18    P(Cross) if HR=1   0.0001
                P(Cross) if HR=0.98   0.0338
      IA 2: 67%                   Z   2.5114
      N: 125558         p (1-sided)   0.0060
  Events: 69461        ~HR at bound   0.9811
      Month: 28    P(Cross) if HR=1   0.0060
                P(Cross) if HR=0.98   0.5603
          Final                   Z   1.9930
      N: 125558         p (1-sided)   0.0231
 Events: 104191        ~HR at bound   0.9877
      Month: 60    P(Cross) if HR=1   0.0250
                P(Cross) if HR=0.98   0.9000



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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a log-rank analysis with a hazard ratio of 0.98, a 95% confidence interval from 0.68 to 1.40, and a p-value of 0.66. This is the reported analysis to use when describing the trial’s result. The posted result also gives the group medians and their confidence intervals, which add an absolute time-based summary to the relative comparison.

No separate recalculated hazard ratio is presented for this result. The registry record’s discrepancy indicator is false, so there is no flagged conflict between the reported result and a recalculated comparison. In general, a recalculation from summary statistics can differ from a sponsor’s analysis because it may not reproduce the original model, data handling, stratification, or event-time information. It should not replace the analysis that uses the trial’s underlying data.

The sponsor’s reported hazard ratio should be interpreted together with its confidence interval and log-rank p-value. The point estimate alone does not show how precisely the effect was estimated, while the p-value alone does not describe the range of compatible effects. Read together, these statistics do not provide strong evidence of a difference in progression-free survival, but they also do not establish equivalence.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is the modified intent-to-treat population, defined in the registry as randomized eligible participants. The endpoint description states that progression-free survival was measured from randomization and that analysis was to occur after progression or death had been reported for 138 participants. The record does not provide a full accounting of exclusions from the randomized population or a participant-flow explanation for the analyzed groups.

The registry lists four secondary outcomes: in-field local failure, development of new lesions, the number of participants by highest grade adverse event reported, and duration of maintenance chemotherapy. Multiple outcomes create the possibility of multiple statistical comparisons. In general, if many hypotheses are tested without an adjustment or prespecified hierarchy, the chance of at least one finding that appears notable by chance can increase. The registry does not report a multiplicity adjustment or a hierarchy for interpreting these secondary outcomes. The primary result should therefore remain distinct from any secondary result.

The primary endpoint description specifies censoring at last known follow-up when no qualifying event has occurred. More detail about missing outcome data, loss to follow-up, censoring patterns by group, or sensitivity analyses is not reported in the registry record. The record also does not describe how incomplete information about disease events was handled.

The registry states the planned analysis threshold of 138 participants with progression or death reported and gives maximum follow-up at analysis as 5.4 years. These details do not establish whether interim efficacy analyses occurred or how monitoring decisions were made; interim analyses are not reported in the registry record. The original statistical analysis plan, including any prespecified subgroup analyses and detailed methods for handling missing data, is also not reported in the registry record.

These omissions limit what can be assessed about the analysis beyond the reported endpoint definition, population, method, and result. They do not invalidate the reported estimate, but they mean that interpretation should stay close to the analysis information available in the registry.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonitis (5.4%), lung infection (4.6%), dyspnea (3.8%), respiratory failure (3.8%), seizure (2.7%).

The registry reports serious adverse events for groups with 73 and 130 participants at risk. Serious adverse events affected 14 participants in the maintenance-only group and 40 in the group receiving local consolidative therapy plus maintenance therapy. The record also reports other adverse events affecting 71 participants among 73 at risk and 129 among 130 at risk, respectively. These are reported counts, not calculated percentages.

Among the serious adverse event terms listed, the most frequent entries include pneumonitis at 5.4%, lung infection at 4.6%, dyspnea at 3.8%, respiratory failure at 3.8%, seizure at 2.7%, and anemia at 2.3%. The record also lists deaths as 37 and 70 in the respective groups. Those death counts should not be interpreted as deaths caused by treatment; the registry entry does not attribute them to treatment.

Safety counts need to be read with their at-risk groups and with care about the event definitions and follow-up. The registry record does not give enough detail in this summary to establish that adverse-event reporting periods or exposure were identical between groups. These figures describe reported events in the posted record; they do not by themselves establish comparative causation or risk.

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

The primary result compares progression-free survival under two treatment strategies: maintenance systemic therapy alone and local consolidative therapy added to maintenance systemic therapy. The reported medians are 11.1 months and 13.7 months, and the sponsor-reported hazard ratio is 0.98. The 95% confidence interval for that relative estimate ranges from 0.68 to 1.40, and the log-rank p-value is 0.66.

These results do not show a clear statistical difference in the primary endpoint. They also do not establish that the strategies have identical effects. The confidence interval includes a range of relative hazard estimates on both sides of 1, and no equivalence or noninferiority objective is reported. A failure to show a clear difference should not be converted into a claim that there is no possible benefit or harm.

The result concerns the endpoint as defined: local or regional disease, distant metastases, a second primary tumor, or death, with censoring at last known follow-up. It does not provide a separate answer for each event type. It is not an overall-survival estimate, and it does not directly establish effects on symptoms, quality of life, or any one listed secondary outcome.

The treatment strategies also included choices among maintenance agents and local treatment approaches. The comparison therefore addresses the strategies as delivered in this trial, rather than the isolated effect of one drug, a specific radiation modality, or surgery alone. The record’s descriptions do not support extending the result to populations or regimens not represented by the trial.

Finally, the result is an estimate based on the registry’s modified intent-to-treat population and follow-up. Its confidence interval expresses uncertainty, and the registry does not provide detailed information about missing data, censoring by group, or the original statistical analysis plan. The most defensible reading is limited: the reported analysis did not demonstrate a clear progression-free survival difference, while leaving uncertainty about the range of relative effects compatible with the data.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two treatment strategies using a randomized design and a time-to-event primary endpoint. Randomization creates a basis for comparing the groups, while progression-free survival incorporates both when events occur and the fact that some participants may be censored before an event is observed. Reporting medians alongside a hazard ratio gives readers complementary summaries of the endpoint.

The result also illustrates why a point estimate should not be read in isolation. The hazard ratio is close to 1, but the confidence interval extends on both sides of 1. The p-value does not provide strong evidence against the null comparison, yet it does not prove that no difference exists. A careful interpretation distinguishes an inconclusive comparison from proof of equal effects.

Several features make transparent reporting especially important. The registry identifies a modified intent-to-treat population, specifies a composite endpoint, gives a planned event threshold, and reports maximum follow-up at analysis. At the same time, it does not report detailed missing-data handling, multiplicity procedures, interim analyses, or the original design assumptions. Those limits affect how thoroughly readers can assess the analysis.

The planning illustrations also show how strongly required event information depends on the size of the effect a future study aims to detect. Smaller target effects require more events under the stated assumptions. Those calculations are planning aids, not a description of the trial’s observed statistical power or its original sample-size rationale.

19. Limitations

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

The registry identifies the phase as phase II while the official title describes a phase II/III trial. The record does not explain the relationship between these labels. The result should be described using the endpoint and analysis actually posted rather than assuming details about a phase transition or study structure that are not reported.

The comparison is between treatment strategies with multiple systemic therapy options and multiple local treatment modalities. The registry descriptions do not establish a uniform regimen for every participant. Consequently, the primary result cannot be attributed to one named drug, radiation technique, or surgical approach in isolation.

The hazard-ratio confidence interval, 0.68 to 1.40, permits a range of relative effects. The result does not establish equivalence, and no equivalence or noninferiority margin is reported. The log-rank p-value of 0.66 should not be used as proof that the groups had the same progression-free survival.

Important analysis details are not reported in the registry record, including the original statistical analysis plan, interim analyses, detailed missing-data handling, censoring patterns by group, and a multiplicity procedure for the secondary outcomes. These gaps limit assessment of the full analysis process. The record gives a maximum follow-up time at analysis of 5.4 years but does not describe the follow-up distribution in detail.

Safety information is also limited to the posted adverse-event counts and listed serious-event terms. The record does not provide, in this summary, enough detail to determine attribution, exposure-adjusted rates, or whether reporting periods were comparable. Death counts should not be taken as treatment-related deaths without attribution information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Maintenance Chemotherapy With or Without Local Consolidative Therapy in Treating Patients With Stage IV Non-small Cell Lung Cancer — NCT03137771.
• Registry record last updated 2026-06-08; status last verified 2026-05.
• Results first posted 2025-03-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03137771 is a randomized, unmasked, parallel-group trial of maintenance systemic therapy with or without local consolidative therapy for stage IV non-small cell lung cancer. The registry lists phase II; the official title describes a phase II/III trial. The stated enrollment is 218, and the current status is active, not recruiting.

The primary endpoint is phase II progression-free survival in the modified intent-to-treat population of randomized eligible participants. The registry reports Kaplan-Meier median estimates of 11.1 months and 13.7 months, with a log-rank hazard ratio of 0.98 (95% confidence interval 0.68 to 1.40; p=0.66). The analysis was planned after progression or death had been reported for 138 participants, and maximum follow-up at analysis was 5.4 years.

The record lists four secondary outcomes and reports adverse-event counts and selected serious adverse-event terms. It does not report the trial’s original sample-size assumptions, interim analyses, detailed missing-data procedures, or multiplicity adjustment.