Cisplatin/Carboplatin and Etoposide With or Without Nivolumab in Treating Patients With Extensive Stage Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cisplatin/Carboplatin and Etoposide With or Without Nivolumab in Treating Patients With Extensive Stage Small Cell Lung Cancer (NCT03382561), a randomized phase 2 study. The primary outcome is Progression-free Survival (PFS).

2. Clinical Question

This was a randomized, open-label, parallel-group phase II trial. The registry lists 160 participants enrolled. Its primary comparison is between the two assigned treatment strategies, while the posted primary outcome analysis includes eligible and treated patients. The registry record does not report why this analysis population was selected instead of all randomized participants.

The clinical question is about the added contribution of nivolumab in a regimen that otherwise includes cisplatin or carboplatin and etoposide. It is not a comparison of the chemotherapy drugs against one another: both arms could receive either platinum drug. The trial also lists overall survival and response rate as secondary outcomes, but the primary statistical question is about time to progression or death.

3. Trial Design

This was a randomized phase II trial with parallel treatment groups and no masking. The National Cancer Institute sponsored the study. The registry describes the trial as completed, with a start date of 2018-05-21 and primary completion on 2022-02-16. Enrollment was 160.

Arm A, labeled CEN, combined nivolumab with cisplatin or carboplatin and etoposide. Nivolumab and the selected platinum drug were given on day 1; etoposide was given on days 1-3. Arm B, labeled CE, used cisplatin or carboplatin and etoposide, with the platinum drug on day 1 and etoposide on days 1-3. The treatment description says cycles repeated every 21 days for up to 4 cycles, subject to disease progression or unacceptable toxicity. The arm A description ends before the corresponding stopping-condition text is complete, so additional detail for that arm is not reported in the registry record.

The posted primary analysis included 75 participants in Arm A and 69 in Arm B. These analysis counts are not the same as the overall enrollment figure; reasons for the difference are not reported in the registry record. The planned allocation ratio and the original target sample-size justification are not reported in the registry record.

Follow-up assessments for the primary outcome were scheduled every 6 weeks for 6 months, then every 8 weeks until 1 year, then every 12 weeks until participants were off treatment or observation ended. The record then describes follow-up every 3 months if less than 2 years from registration, every 6 months for years 2-3, and yearly up to 3 years 9 months. The registry record does not report whether interim analyses were planned or conducted.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Eligible and treated patients were included in the analysis.

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: All randomized patients

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival (PFS), measured over Every 6 weeks for 6 months, then every 8 weeks until 1 year, and then every 12 weeks until being off treatment or end of observation. Thereafter every 3 months if < 2 years from registration, every 6 months for years 2-3, and yearly up to 3 years 9 months.

The primary endpoint was progression-free survival (PFS), measured in months. PFS is a time-to-event outcome: it measures the time from randomization until documented disease progression or death from any cause, whichever happens first. Participants without an event by the time of analysis were censored at the date they were last known to be alive and progression-free.

Progression was assessed using the revised Response Evaluation Criteria in Solid Tumors, version 1.1. The registry definition includes the appearance of one or more new lesions, unequivocal progression of existing non-target lesions, or an increase of at least 20% in the sum of target-lesion diameters relative to the smallest sum on study, with an absolute increase of at least 5 mm.

PFS is used to summarize how long participants remain alive without documented progression. It captures progression as well as death, rather than requiring death to occur before an event is counted. That makes it distinct from overall survival, which is listed as a secondary outcome. Because participants may be censored if they have no recorded event by analysis, the time-to-event methods also depend on how follow-up and censoring are handled. Further details of the censoring analysis beyond the stated definition are not reported in the registry record.

7. Results Posted in the Registry

• Arm A (Cisplatin/Carboplatin, Etoposide and Nivolumab; CEN) vs Arm B (Cisplatin/Carboplatin and Etoposide; CE): hazard ratio 0.78 (95% CI 0.55–1.11), reported p = 0.170 (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.

Response Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B (Cisplatin/Carboplatin and Etoposide; CE): 1.4% (1/69) versus 1.3% (1/75) on control; risk difference 0.1 percentage points (95% CI -3.7 to 3.9), risk ratio 1.09 (0.07–17.04); unadjusted two-proportion z-test p = 0.953.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Cisplatin/Carboplatin and Etoposide; CE) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists overall survival and response rate as secondary outcomes. The posted record includes response-rate results, but it does not include overall survival result values; those results are not reported in the registry record. The secondary information therefore provides only a partial view of outcomes beyond PFS.

Broadly, the secondary endpoint record does not add a clearly documented sponsor-reported comparison that resolves the uncertainty in the primary PFS result. Response rate is a different kind of outcome from PFS: it records whether a response occurred, while PFS accounts for time to progression or death and incorporates censoring. The two endpoints can complement one another, but they do not measure the same clinical course. The absent overall survival results further limit the extent to which secondary outcomes can inform interpretation of the primary finding.

Secondary analyses generally carry less weight than a prespecified primary analysis, particularly when several endpoints are examined. Testing multiple outcomes can increase the chance of at least one apparently notable result by chance if no multiplicity procedure is used. Whether and how multiplicity was controlled is not reported in the registry record. The response comparison is not reported as a sponsor analysis, so its unadjusted recalculation should be regarded as descriptive and exploratory rather than confirmatory.

These endpoints should be considered as separate pieces of evidence, with attention to their definitions, analysis methods, and uncertainty. The record does not provide enough detail to establish a complete hierarchy of secondary hypotheses or to know how the investigators intended to interpret them alongside PFS.

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

• Overall Survival (OS)
• Response Rate

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure, so its analysis differs from a comparison of simple proportions. Each participant contributes a duration of observation and, if an event occurs, an event status. Participants who have not had progression or died by the analysis date are censored at their last known time alive and progression-free, as described in the registry record. Censoring allows participants with incomplete follow-up to contribute information up to their last known event-free time, rather than treating their eventual outcome as known.

What does the median PFS describe?

A median time-to-event value is the point at which the estimated event-free survival curve reaches its midpoint. It provides an interpretable summary in months, but it does not summarize every feature of the curve. Two groups can have similar medians while differing at other follow-up times, or have different medians while their uncertainty overlaps. The registry reports medians and confidence intervals for both arms, but does not provide additional curve-level summaries in the stated details.

What does the hazard ratio describe?

The sponsor reported a hazard ratio from a log-rank analysis. In general, a hazard ratio compares event rates over follow-up under the analysis model; it is not a ratio of median PFS values and should not be read as a direct difference in months. A value below 1 is oriented toward a lower event hazard for the first-listed arm, while a value above 1 is oriented toward a higher event hazard. This interpretation assumes the comparison is understood in the stated arm order. The registry record does not report whether the proportional-hazards assumption was assessed or what other model checks were made.

The log-rank test is a standard method for comparing time-to-event experience between groups. It uses the timing of events and the risk sets over follow-up, rather than comparing only the two medians. A p-value summarizes how incompatible the observed data are with a specified null hypothesis under the test’s assumptions; it does not give the probability that the null hypothesis is true. The sponsor reported p = 0.17 for the primary comparison. Further details of the test implementation, including any stratification factors, are not reported in the registry record.

How should the confidence intervals be read?

A confidence interval conveys uncertainty around an estimate under the statistical procedure used. For the primary hazard ratio, the interval runs from 0.55 to 1.11. Since it includes 1, the data are compatible with no hazard ratio difference as well as with effects on either side of 1. The interval’s range is important alongside the point estimate: it shows that the estimated direction does not pin down the size or direction of the underlying comparative effect precisely.

The arm-specific median confidence intervals describe uncertainty around each median separately. They are not a substitute for a confidence interval on the difference between arms or for the hazard ratio interval. Overlap or non-overlap between two arm-specific intervals is not itself the reported test of the treatment comparison.

Why can a binary outcome have a different analysis?

Response rate is a binary outcome: each participant is classified according to whether a response was observed under the endpoint definition. A comparison of proportions therefore differs from the primary time-to-event analysis. The registry lists response rate as a secondary outcome and posts arm-level proportions with confidence intervals. The comparative calculations associated with those proportions are unadjusted re-calculations from posted summary information; the registry does not list a sponsor-reported comparative response analysis. Such re-calculations do not replace a prespecified sponsor analysis.

Over-dispersion is a general concern when observed variation exceeds what a simple statistical model assumes. If present, standard errors can be too small and confidence intervals too narrow under a model that fails to account for that extra variation. The registry record does not report an over-dispersion assessment for the response outcome, nor does the available record establish that this concern affected the analysis.

What analysis details remain unclear?

The record states that eligible and treated participants were included in the PFS analysis, but does not report the complete statistical analysis plan, the original sample-size justification, handling of protocol deviations, or the method for addressing missing outcome data beyond the stated censoring rule. It also does not report interim analyses, proportional-hazards checks, or a multiplicity adjustment. These omissions limit how fully an independent reader can evaluate the analysis choices. They do not change the values reported in the registry, but they do make the results less fully reproducible from the record alone.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is bounded by its uncertainty interval. For the sponsor-reported PFS hazard ratio, the estimate is 0.78 and the 95% confidence interval extends from 0.55 to 1.11. The interval includes 1, the value corresponding to no relative hazard difference, and also includes values above 1. Thus, the estimate does not establish a single direction of effect with high precision.

The arm-specific median PFS estimates also have confidence intervals: 4.3 to 5.9 months for Arm A and 4.5 to 5.7 months for Arm B. These intervals reflect uncertainty around each arm’s median, not a direct interval for a median difference. The observed medians are close, but the principal comparative estimate is the sponsor-reported hazard ratio and its interval.

In general, a 95% confidence interval is generated by a method designed to cover the underlying value in 95% of repeated samples under its assumptions. It is not a statement that there is a 95% probability that the particular fixed effect lies within this particular interval. Its interpretation also depends on the analysis model and study conduct, details of which are not fully reported in the registry record.

The interval’s inclusion of both sides of 1 means that the data leave room for materially different comparative interpretations. The point estimate alone would conceal this uncertainty. Precision should therefore be considered together with the estimate, the p-value, the analysis population, and the limits of the registry record. The result is not precise enough to treat the point estimate as a settled effect.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design calculation. The assumptions stated for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. For the time-to-event outcome, the figures represent total events, using the Schoenfeld approach; for other outcomes, the figures represent participants per arm.

Accordingly, the PFS planning rows should be read as total events needed for 80% or 90% power under each assumed effect size. They are not counts of participants per arm. The response-rate planning rows instead give participants per arm for 80% power and participants per arm for 90% power. In plain terms, the 80% column describes a planning target under which the assumed design would have an 80% chance of detecting the specified effect at the stated significance level, if the assumptions hold. The 90% column uses a higher probability of detecting that effect, and therefore requires a larger planning target under otherwise comparable assumptions.

The effect fractions describe planning for 100%, 75%, or 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more events or participants. The figures are not observed power and do not describe the probability that the completed trial’s result is true or reproducible. The registry record does not report the trial’s own original sample-size assumptions or justification.

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 = 0.780, so ln(HR) = -0.2485.
2. d = 4 × (1.96 + 0.842)² / [ln(0.780)]² = 508.6, rounded up to 509 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 <- 0.78                              # 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(3382561)
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 = 509 (80% power), 681 (90% power)
 75% of observed effect: events = 905 (80% power), 1,211 (90% power)
 50% of observed effect: events = 2,035 (80% power), 2,724 (90% power)
Simulated power with 509 events: 0.796 (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 746 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 160 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 <- 4.9          # control-arm median, months (converted from the posted unit)
hr          <- 0.78          # 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: 446         p (1-sided)   0.0001
 Events: 230        ~HR at bound   0.6127
   Month: 14    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.78   0.0338
   IA 2: 67%                   Z   2.5114
      N: 718         p (1-sided)   0.0060
 Events: 459        ~HR at bound   0.7910
   Month: 23    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.78   0.5603
       Final                   Z   1.9930
      N: 746         p (1-sided)   0.0231
 Events: 689        ~HR at bound   0.8590
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.78   0.9000



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

15. Analyses Reported by the Sponsor

The primary comparison uses the sponsor-reported log-rank hazard ratio, confidence interval, and p-value. These are the appropriate primary comparative results to interpret from the registry record. There is no recalculated primary hazard ratio replacing the sponsor’s analysis. The posted medians describe each arm separately, while the reported hazard ratio summarizes the sponsor’s comparative time-to-event analysis.

For response rate, the registry does not list a sponsor-reported comparative analysis. Any comparative figures derived from the posted arm-level summaries are unadjusted re-calculations, not the sponsor’s own inferential analysis. They should therefore be read as simple calculations from summary data and not as substitutes for a prespecified analysis. The sponsor’s original statistical approach for that endpoint is not reported in the registry record.

The registry record does not flag a discrepancy between the sponsor-reported primary analysis and a recalculation. More generally, differences in analysis methods, populations, or assumptions can lead to different estimates; those details should be kept distinct rather than combining estimates as if they came from one analysis.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis considers more than one outcome, comparison, subgroup, or time point. Repeated testing can raise the chance of finding at least one result that appears statistically notable even when the underlying effects are absent. A prespecified approach may control that risk, but the registry record does not report a multiplicity adjustment or a testing hierarchy for the primary and secondary outcomes.

The registry names PFS as the primary endpoint and lists overall survival and response rate as secondary outcomes. It also describes repeated outcome assessment during follow-up. The presence of more than one endpoint or assessment does not by itself establish that statistical multiplicity was a problem, but it makes the analysis plan relevant. Whether any adjustments were made, and how the primary and secondary tests were ordered, are not reported in the registry record.

The PFS analysis population is described as eligible and treated patients. The record does not report how many randomized participants were excluded from that analysis, why any participants were excluded, or how treatment discontinuations and protocol deviations were handled. The overall enrollment is 160, while the posted PFS arm counts are 75 and 69. The registry record does not explain the difference between these counts.

For PFS, participants without an event by analysis were censored at their last known date alive and progression-free. Further information about missing assessments, loss to follow-up, censoring patterns, or sensitivity analyses is not reported in the registry record. These details matter because time-to-event estimates rely on follow-up being handled appropriately. The record also does not report the analysis population for every secondary endpoint, the original sample-size justification, interim analyses, or the full statistical analysis plan. These omissions limit assessment of prespecification and robustness.

17. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: neutrophil count decreased (51.4%), anemia (22.1%), white blood cell decreased (21.6%), platelet count decreased (18.2%), lymphocyte count decreased (17.6%).

The registry reports serious adverse event summaries for both arms. In Arm A, 59 of 77 participants at risk were recorded as having a serious adverse event; in Arm B, the corresponding figures were 49 of 74. For other adverse events, 76 of 77 participants at risk in Arm A and 73 of 74 in Arm B were recorded as affected. The death counts are 67 for Arm A and 74 for Arm B.

These group-level counts describe participants recorded as affected and the numbers at risk in each adverse-event group. They do not, on their own, identify the cause of an event or establish that treatment caused it. The registry record does not provide additional causal attribution or details needed to interpret the death counts as treatment-related.

The most frequently listed serious adverse event terms include neutrophil count decreased (51.4%), anemia (22.1%), white blood cell decreased (21.6%), platelet count decreased (18.2%), lymphocyte count decreased (17.6%), and fatigue (13.0%). These are the posted percentages for the listed terms; the record does not give the term-specific denominators in the registry record presented. Comparisons between arms should not be inferred from these aggregate summaries alone.

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

The primary result is an estimate of the comparison in progression-free survival between the two randomized treatment groups among eligible and treated participants. The sponsor-reported hazard ratio is 0.78, with a 95% confidence interval from 0.55 to 1.11 and p = 0.17. The point estimate is numerically below 1, but the interval includes 1 and extends above it. The result therefore leaves substantial uncertainty about the direction and size of the comparative effect.

The arm-specific median PFS values provide additional description, but they do not by themselves determine whether the treatment strategies differ. The confidence intervals for the medians also describe uncertainty in each group’s median rather than a direct interval for their difference. The sponsor’s hazard ratio and its uncertainty are the central comparative summary reported for the primary endpoint.

The result does not prove that the treatment strategies are equivalent, because the analysis is not an equivalence or non-inferiority analysis and no such margin is reported. It also does not establish that one regimen is superior. A p-value of 0.17 is not the probability that there is no effect, and a confidence interval that includes 1 should not be interpreted as proof of no difference.

The secondary record is incomplete for broader outcome interpretation: response rate is posted, while overall survival values are not reported in the registry record. The record also does not describe multiplicity adjustment, all missing-data procedures, or the full analysis plan. These limitations matter when judging how much weight to place on any single estimate. The statistics describe the posted trial results; they do not provide medical advice or a basis for individual treatment decisions.

19. Why This Trial Matters Statistically

This trial raises a statistical question that is common in randomized clinical research: how to interpret a treatment comparison when the point estimate has a direction but its confidence interval spans both sides of the null value. The PFS hazard ratio is numerically below 1, but its interval extends from 0.55 to 1.11. Reporting the estimate together with the interval and p-value makes the uncertainty more visible than relying on the point estimate alone.

The trial also illustrates why the type of endpoint matters. PFS combines progression and death over time and uses censoring for participants without an event at analysis. Response rate is instead a binary outcome, and overall survival is a separate time-to-event outcome. These measures offer different information and should not be treated as interchangeable evidence.

Another statistical issue is the distinction between a sponsor-reported primary analysis and calculations based on posted summaries. The sponsor’s log-rank result is the primary comparative analysis available for PFS. Unadjusted calculations for a secondary endpoint are not equivalent to a prespecified sponsor analysis. Keeping those sources separate helps readers avoid overstating what the record supports.

Finally, the registry lists 160 enrolled participants but reports smaller analysis counts for PFS. The record does not explain that difference. Clarity about analysis populations, missing outcome data, multiplicity, and sample-size planning is important for evaluating the strength and reproducibility of trial findings. The available record supports a careful description of the estimates, while leaving some methodological questions unresolved.

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 original sample-size justification, the intended allocation ratio, or the assumptions used when the trial was designed. Planning illustrations based on the observed effect cannot substitute for those original design details. The record also does not describe interim analyses or provide a complete statistical analysis plan.

Although the trial was randomized, the posted PFS analysis included eligible and treated participants. The record does not explain why the analysis counts differ from overall enrollment, or whether all randomized participants were analyzed according to their assigned group. This limits assessment of the consequences of exclusions and treatment deviations.

The primary result is reported with a hazard ratio and log-rank p-value, but additional analysis details are not reported in the registry record. These include whether proportional hazards were assessed, whether the analysis was stratified, and whether sensitivity analyses were conducted. Censoring is described, but missing assessments, follow-up completeness, and reasons for censoring are not detailed.

The registry lists secondary outcomes, but overall survival result values are not reported in the registry record. The response comparison lacks a sponsor-reported analysis in the posted information, and no multiplicity procedure is described. Finally, the arm A treatment description is incomplete at its ending, so its stopping-condition wording cannot be fully compared with the arm B description from the record. These limitations do not invalidate the reported statistics, but they restrict how completely the analysis can be assessed.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Cisplatin/Carboplatin and Etoposide With or Without Nivolumab in Treating Patients With Extensive Stage Small Cell Lung Cancer — NCT03382561.
• Registry record last updated 2025-07-03; status last verified 2025-06.
• Results first posted 2023-06-23.
• 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

NCT03382561 is a completed, randomized, open-label, parallel-group phase II trial sponsored by the National Cancer Institute. It enrolled 160 participants and compared cisplatin or carboplatin plus etoposide with the same chemotherapy combined with nivolumab for extensive stage small cell lung cancer.

The primary endpoint was PFS. The sponsor-reported comparison used a log-rank analysis and reported a hazard ratio of 0.78, a 95% confidence interval from 0.55 to 1.11, and p = 0.17. The analysis population was eligible and treated participants. The registry also lists response rate and overall survival as secondary outcomes; overall survival result values are not reported in the registry record.

The record gives adverse-event summaries and arm-specific PFS medians, but does not report several design and analysis details, including the original sample-size justification, interim analyses, and a complete multiplicity approach. The findings should be interpreted with attention to the uncertainty in the primary estimate and the limits of the registry information.