A Dose Frequency Optimization,Trial of Nivolumab 240 mg Every 2 Weeks vs Nivolumab 480 mg Every 4 Weeks in Subjects With Advanced or Metastatic Non-small Cell Lung Cancer Who Received Up to 12 Months of Nivolumab at 3 mg/kg or 240 mg Every 2 Weeks: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Dose Frequency Optimization,Trial of Nivolumab 240 mg Every 2 Weeks vs Nivolumab 480 mg Every 4 Weeks in Subjects With Advanced or Metastatic Non-small Cell Lung Cancer Who Received Up to 12 Months of Nivolumab at 3 mg/kg or 240 mg Every 2 Weeks (NCT02713867), a randomized phase 3 study. The primary outcome is Progression Free Survival Rate (PFSR) at 6 Months.

2. Clinical Question

The endpoint combines two clinical events: disease progression and death. A participant counts as progression-free and surviving at the assessment time only if neither event has occurred by then, according to the endpoint definition. Participants without progression or death may be censored at the date of their last evaluable tumor assessment, so their status is not treated as known beyond that assessment.

The question is about whether the dosing interval can be changed while describing outcomes in this specific clinical setting. It is not a comparison of whether nivolumab is better than another treatment. Nor does the endpoint, by itself, establish that the schedules are equivalent or interchangeable. That would require an explicitly defined inferential framework and criteria; such details are not reported in the registry record.

3. Trial Design

The registry record describes a randomized, parallel-group trial with no masking. Participants were assigned to nivolumab 480 mg every 4 weeks or nivolumab 240 mg every 2 weeks. The study title identifies the trial as Phase IIIB/IV, while the registry phase category is Phase 3. The sponsor is Bristol-Myers Squibb.

The trial enrolled 363 participants. Its condition is listed as lung cancer, and its title and summary specify advanced or metastatic non-small cell lung cancer, including non-squamous and squamous disease. The population was not described as newly starting nivolumab: participants had received up to 12 months of nivolumab at 3 mg/kg or 240 mg every 2 weeks before randomization. The posted primary endpoint population is all randomized participants.

The registry lists a start date of 2016-05-24, a primary completion date of 2019-07-15, and a completed status. Those record details describe the trial's registration and progress; they do not supply additional outcome results or explain the analysis choices.

Random allocation supports a comparison of outcomes between the assigned schedules, provided that follow-up, outcome assessment, and analysis are handled appropriately. The parallel structure means the posted arm outcomes are presented separately for each assigned regimen. With no masking, participants and study staff were not masked to treatment assignment according to the registry entry. This could be relevant to outcomes involving judgment or reporting, although progression criteria are described using tumor assessments and explicit rules.

The registry record does not report the trial's original sample-size justification, allocation ratio rationale, randomization implementation details, interim analyses, or a full statistical analysis plan. It also does not report details sufficient to establish how departures from assigned dosing were handled. Those omissions limit what can be concluded about the planned inferential framework beyond the outcome descriptions and posted summaries.

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.

Randomization

Reasons for not completing this period:

Treatment Period

Reasons for not completing this period:

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

6. Primary Endpoint

The registry lists the primary outcome as Progression Free Survival Rate (PFSR) at 6 Months, measured over At 6 Months.

The primary endpoint is the progression-free survival rate at 6 months, expressed as a proportion of participants. It represents the proportion who are alive and have not had disease progression by the specified assessment time. The endpoint description says that participants who did not progress or die are censored on the date of their last evaluable tumor assessment.

Progression is defined using target-lesion measurements: at least a 20% increase in the sum of diameters, relative to the smallest sum on study, together with an absolute increase of at least 5 mm. The appearance of one or more new lesions also counts as progression. These criteria make the event definition more explicit than a general clinical impression of worsening disease.

A fixed-time rate is useful for communicating the share of participants meeting the endpoint at a clinically specified time. It offers a direct description of status at 6 months, but it does not show the full timing of progression or death. Two groups can have similar fixed-time rates while differing in when events occurred, and censoring means that follow-up information is not necessarily available for every participant through the assessment time.

The registry reports arm-level proportions with 95% confidence intervals. The registry record does not describe a time-to-event model for this primary result, the method used to estimate the fixed-time rates, or how missing tumor assessments were handled beyond the stated censoring rule. Those details matter when interpreting precision and the assumptions underlying the estimates.

7. Results Posted in the Registry

• Nivolumab 240mg: 0.5% (1/183) versus 0.6% (1/180) on control; risk difference -0.0 percentage points (95% CI -1.5 to 1.5), risk ratio 0.98 (0.06–15.61); unadjusted two-proportion z-test p = 0.991.

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.

Progression Free Survival Rate (PFSR) at 24 Months

• 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:
  • Nivolumab 240mg: 0.5% (1/183) versus 0.6% (1/180) on control; risk difference -0.0 percentage points (95% CI -1.5 to 1.5), risk ratio 0.98 (0.06–15.61); unadjusted two-proportion z-test p = 0.991.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab 240mg and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival (OS) Rate at 12 Months

• 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:
  • Nivolumab 240mg: 0.7% (1/150) versus 0.7% (1/142) on control; risk difference -0.0 percentage points (95% CI -1.9 to 1.9), risk ratio 0.95 (0.06–14.99); unadjusted two-proportion z-test p = 0.969.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab 240mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Who Experienced Death

• 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:
  • Nivolumab 240mg: 43.9% (79/180) versus 49.4% (88/178) on control; risk difference -5.5 percentage points (95% CI -15.9 to 4.8), risk ratio 0.89 (0.71–1.11); unadjusted two-proportion z-test p = 0.293.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab 240mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary fixed-time progression-free assessment to later progression-free status, overall survival, outcomes by histology or response criteria, and adverse events. They therefore provide a broader account of the trial experience, but they do not all measure the same construct. Progression-free status and overall survival are distinct endpoints, while adverse-event summaries address safety rather than tumor control.

Across the posted secondary arm estimates, the results offer additional descriptive context for the dosing comparison. They should be interpreted alongside the primary result rather than as replacements for it. Later outcomes may reflect longer follow-up and different amounts of available information; the registry record does not provide sufficient detail to assess completeness of follow-up across these outcomes.

The record lists 15 secondary outcomes and no reported analyses. In particular, it does not document an analysis hierarchy, multiplicity adjustment, or a prespecified strategy for interpreting the family of secondary comparisons. If many outcomes are tested, some apparently unusual results can occur by chance even when no corresponding effect exists. This general issue means that unadjusted secondary results carry less evidential weight than a single prespecified primary analysis, especially when the analysis plan is not available.

Secondary results can still be useful for generating hypotheses, identifying patterns that merit further study, and describing outcomes beyond the primary assessment time. They cannot independently establish a treatment-schedule effect without careful attention to endpoint definition, censoring, analysis population, and multiplicity. The registry record does not report enough methodological detail to determine how these matters were handled for every outcome.

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

• Progression Free Survival Rate (PFSR) at 24 Months
• Progression Free Survival Rate (PFSR) by Tumor Histology at 12 Months
• Progression Free Survival Rate (PFSR) by Response Criteria at 12 Months
• Overall Survival (OS) Rate at 12 Months
• Overall Survival (OS) Rate up to 60 Months
• Overall Survival Rate by Histology at 12 Months
• Overall Survival Rate by Response Criteria at 12 Months
• Percentage of Participants With an Adverse Events (AEs)

9. Statistical Interpretation

10. Statistical Methods Explained

Randomization assigns participants to treatment groups by chance, which is intended to make the groups comparable at the start of the comparison. It can reduce confounding by measured and unmeasured characteristics on average, but it does not guarantee identical groups in a particular trial. The registry identifies this study as randomized and parallel-group. It does not report the method used to generate or conceal the allocation sequence.

What does a fixed-time proportion describe?

A fixed-time proportion reports the share of participants meeting a defined outcome at a particular time. For this primary endpoint, the outcome requires both being alive and having no progression at 6 months. This is different from reporting the time until the first event for each participant. It is also different from reporting the number of events alone, because a proportion depends on the denominator and on how censoring and missing observations are handled.

The endpoint description sets out tumor-based progression criteria and a censoring rule for participants without progression or death. Censoring is a statistical way to retain information up to the last known assessment without treating later status as known. Its validity depends on assumptions about why follow-up ends. The registry record does not report enough detail to assess those assumptions or explain how the fixed-time rate estimator treats censored observations.

How should the arm estimates and contrast be read?

The arm-level rates are direct summaries of each assigned group, accompanied by 95% confidence intervals. The interval communicates sampling uncertainty under the estimation method. It does not include all uncertainty arising from endpoint measurement, missing data, protocol deviations, or limitations in the registry record.

A risk difference expresses an absolute contrast between proportions, while a relative risk expresses a ratio. A confidence interval for a contrast describes values compatible with the data under the specified method. A p-value summarizes how surprising data at least as extreme as the observed data would be under a null hypothesis and model assumptions. It is not a measure of effect size, a probability that the null hypothesis is true, or evidence of equivalence by itself.

In this record, the arm-level primary estimates are 0.76 and 0.79, while the comparison fields report a risk difference of -< 0.001 and a p-value of 0.991. Those summaries do not appear to represent the same contrast. Readers should not combine them as if they were mutually confirming outputs. The registry record contains no reported sponsor analysis to resolve the mismatch, and no analysis is listed in the record.

Why does lack of masking matter?

Masking can limit the influence of knowledge about treatment assignment on care, reporting, and assessment. The registry lists no masking. The primary endpoint includes tumor assessments, with progression defined by measurement rules, which makes the outcome more structured than a purely subjective rating. Still, the record does not explain whether tumor assessments were independently reviewed or whether outcome assessors were masked. Such procedures are not reported in the registry record.

More frequent or less frequent dosing could also affect participant experience and clinical contact, but the record does not describe those processes. That possibility is a general consideration, not a claim that it affected these results.

What can secondary analyses add?

Secondary outcomes can broaden the description of the trial, for example by reporting later progression-free status, overall survival, and adverse events. Each outcome answers a different question and may have a different analysis population or amount of follow-up. The record posts 15 secondary outcomes and reports no analyses for them. Without a reported statistical analysis plan, it is not possible to determine which comparisons were prespecified, how outcomes were prioritized, or whether methods were selected after examining the data.

When many outcomes are examined, the chance of observing apparently notable findings by chance increases. Multiplicity adjustments or a prespecified hierarchy can address this issue, but whether either was used is not reported in the registry record. Unadjusted p-values for secondary outcomes, where available, should therefore be interpreted as exploratory rather than as independent confirmation of the primary finding.

What does a sample-size planning illustration mean?

The registry's planning illustration is based on the observed effect and uses a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. It considers the stated fraction of the observed effect. The original trial design assumptions and original sample-size justification are not reported in the registry record. The illustration is not an account of the trial's design and is not observed power.

Power is the probability, under a specified effect and set of assumptions, that a test will reject a stated null hypothesis. The 80% and 90% columns translate those planning assumptions into the number of participants per arm for the binary outcomes. These projections depend strongly on the effect size chosen. Smaller effects require more participants to detect with the same power, all else equal. The values should be read as hypothetical planning requirements under the stated assumptions, not as a retrospective measure of whether the completed trial succeeded.

11. Confidence Intervals and Precision

The primary arm estimates are accompanied by 95% confidence intervals. For nivolumab 480 mg every 4 weeks, the rate is 0.76 and the interval is 0.70 to 0.83. For nivolumab 240 mg every 2 weeks, the rate is 0.79 and the interval is 0.73 to 0.85. These intervals express uncertainty around each arm estimate, not certainty about an individual participant's outcome.

Confidence intervals are useful because they show a range of estimates compatible with the observed data and the method's assumptions. Their width is one indication of precision: a narrower interval generally indicates less sampling uncertainty than a wider interval. Precision is not the same as validity. An estimate can be precise yet affected by bias, incomplete follow-up, or limitations in the outcome definition.

The comparison fields report a risk difference of -< 0.001 and a 95% confidence interval from -0.015 to 0.015. This comparison summary appears inconsistent with the arm-level estimates, so its apparent precision should not be treated as a dependable description of the arm-level contrast. No sponsor analysis is reported in the registry record to clarify the difference.

Intervals around arm-level proportions do not directly provide an interval for the difference between arms. A formal contrast interval must be calculated using an appropriate method, and the method should be consistent with the outcome data. The registry record does not report enough detail to evaluate how the comparison interval was generated. Nor does the absence of a statistically small p-value establish equivalence; an equivalence or non-inferiority conclusion requires a prespecified margin and analysis framework, which are not reported in the registry record.

General interpretation: confidence intervals describe statistical uncertainty under a model, while clinical importance depends on the meaning of the outcome and the magnitude of a difference that would matter in the relevant setting. The registry does not report a clinically important difference threshold for this endpoint.

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 sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculation. For the binary outcomes in this analysis, the figures are participants per arm, rather than total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustration considers the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the projected number of participants per arm under the stated assumptions to have an 80% chance of detecting the effect used for planning, if that effect and the assumptions were correct. The 90% column gives the corresponding projection for a 90% chance. Higher target power generally requires more participants, all else equal. Smaller effects also require more participants because they are harder to distinguish from random variation.

Rows that plan for a fraction of the observed effect ask what sample size would be needed if the true effect were smaller than the observed one. Those projections can become extremely large when the observed contrast is small. They should not be read as evidence that a trial of that size would be necessary in practice without considering a justified target effect, design, outcome, and analysis plan.

This is not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a trial is completed. The planning figures are hypothetical calculations conditional on the stated assumptions; they do not revise the trial's actual enrollment or demonstrate that the trial had adequate precision for every scientific question.

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

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.006; treatment proportion p₁ = 0.005; average p̄ = 0.006.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1047 = 0.2052.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1047 = 0.0881.
4. n = (0.2052 + 0.0881)² / (-0.0001)² = 10,370,405.7, rounded up to 10,370,406 participants per arm 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
p0 <- 0.00555555555555556                          # control proportion
p1 <- 0.00546448087431694                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2713867)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 10,370,406 (80% power), 13,883,031 (90% power)
 75% of observed effect: n per arm = 18,474,158 (80% power), 24,731,656 (90% power)
 50% of observed effect: n per arm = 41,652,085 (80% power), 55,760,324 (90% power)
power.prop.test: 10370406 
Simulated power at n = 10,370,406 per arm: 0.796 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or statistical tests are considered. Even if each test is conducted using a conventional threshold, examining a collection of tests increases the chance that at least one result will appear noteworthy by chance. This is a general statistical concern and does not imply that any particular result in this trial is false.

The registry lists 15 secondary outcomes, including progression-free survival at a later time, outcomes by tumor histology or response criteria, overall survival measures, and adverse events. The record reports no analyses for these secondary outcomes. It does not describe a multiplicity adjustment, a testing hierarchy, or a plan that distinguishes confirmatory from exploratory outcomes. These details are not reported in the registry record.

The primary endpoint is identified as progression-free survival rate at 6 months. The brief summary also describes comparison at 1 year, but the listed primary outcome is the 6-month rate. The registry record does not explain whether the 1-year objective was handled as a co-primary endpoint, a key secondary endpoint, or another planned analysis. That distinction matters because it affects how results across time points should be interpreted.

Other important analysis details are also not reported in the registry record. These include the original sample-size justification, the analysis population for each outcome beyond the primary endpoint's stated all-randomized population, the handling of missing observations beyond the endpoint censoring description, and the statistical methods used for the posted estimates. The record does not report interim analyses or a full statistical analysis plan.

When methods and analysis populations are not fully documented, readers cannot determine whether every analysis followed a prespecified plan or assess the impact of missing information and exclusions. The absence of these details does not itself show that the analyses were inappropriate. It does limit reproducibility and makes cautious interpretation particularly important for secondary and subgroup findings.

15. 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: pneumonia (5.0%), malignant neoplasm progression (5.0%), chronic obstructive pulmonary disease (3.9%), diarrhoea (2.2%), pneumonitis (2.2%).

The serious adverse-event summaries report 62 affected participants among 178 at risk in the nivolumab 480 mg group and 71 among 180 at risk in the nivolumab 240 mg group. These are counts with their stated risk-set denominators; they should not be confused with the primary efficacy population sizes or with the separate death outcome.

The registry also lists serious-event terms and percentages, including pneumonia at 5.0%, malignant neoplasm progression at 5.0%, chronic obstructive pulmonary disease at 3.9%, diarrhoea at 2.2%, pneumonitis at 2.2%, and pulmonary embolism at 2.2%. The record does not specify in this summary whether these term percentages are presented by arm or under another grouping, so they should not be assigned to an arm without further information.

Adverse-event counts describe what was recorded during the trial, not necessarily what was caused by a dosing schedule. The registry reports no comparative safety analysis, adjustment for exposure time, or detailed event definitions in the posted summary. The separate death outcome has its own observation window and should not be treated as interchangeable with a serious adverse event.

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

The registry describes a randomized comparison of two nivolumab schedules in participants with advanced or metastatic non-small cell lung cancer who had already received nivolumab before randomization. The posted primary outcome reports progression-free survival rates at 6 months for each group, with confidence intervals. Those estimates describe the trial participants' observed outcomes under the endpoint definition and follow-up available for the analysis.

The primary comparison fields report a risk difference close to zero, a confidence interval spanning values on either side of zero, and an unadjusted p-value of 0.991. However, that comparison summary does not appear consistent with the posted arm-level proportions. The registry record does not report a sponsor analysis that reconciles them. The comparison should not be treated as a clear, reliable test of the arm-level rates without that clarification.

Even if a comparison were internally consistent, a non-significant p-value would not prove that the schedules are equivalent. Equivalence requires a prespecified margin defining how large a difference would still count as acceptably similar, along with an analysis designed to test that claim. A non-inferiority conclusion similarly requires a prespecified margin and appropriate methods. Neither margin nor framework is reported in the registry record.

The endpoint is a fixed-time rate, so it does not convey the full timing of progression or death. Censoring and missing assessments can affect what is known at the assessment time, and the registry gives limited information about missing-data handling. The posted results also do not establish how the findings would apply to people outside the enrolled population or to different treatment contexts.

Accordingly, the results can be read as descriptive estimates from a randomized schedule comparison, with substantial limits on inferential interpretation. They do not by themselves establish that either schedule is preferable, that the schedules are interchangeable, or that a particular treatment decision is appropriate.

17. Why This Trial Matters Statistically

This trial addresses a statistical question that is easy to state but not always easy to answer: whether outcomes observed under two dosing schedules can be compared precisely enough to support a conclusion about their similarity or difference. Randomization and a parallel-arm design provide a framework for that comparison, while the fixed-time progression-free endpoint gives a clinically interpretable summary at a specified assessment time.

The example also shows why arm estimates and comparison statistics need to be checked together. The posted primary rates are accompanied by arm-specific confidence intervals, but the reported contrast does not appear to align with those arm estimates. A p-value alone cannot resolve such a mismatch. Clear reporting of the estimator, analysis population, censoring approach, and derivation of the contrast is important for readers who need to understand what the statistics represent.

Planning illustrations based on observed effects have a different role from the sample-size justification used to design a trial. They can demonstrate how strongly required sample size depends on the target effect, but cannot establish whether the completed trial was adequately planned or powered. In this case, the original design assumptions are not reported in the registry record.

The registry also illustrates the importance of distinguishing a primary endpoint from a broad set of secondary outcomes. Secondary results can add context, but multiplicity and incomplete analysis-plan reporting affect the weight they can carry. Statistical interpretation depends not only on the numerical estimates, but also on transparent methods and a prespecified framework.

18. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the original sample-size calculation, the assumptions underlying the trial's design, or a full statistical analysis plan. Consequently, the planning illustrations based on the observed effect cannot be used to judge the study's original design rationale.

The primary comparison fields appear inconsistent with the posted arm-level proportions. No sponsor analysis is reported to resolve that issue. This limits confidence in using the listed contrast estimate, confidence interval, and p-value as a summary of the primary comparison.

The registry identifies no masking. It does not report whether tumor assessments were independently reviewed or whether assessors were masked, nor does it describe allocation concealment. Those procedures are not reported in the registry record, so their potential role cannot be evaluated.

The primary endpoint definition includes censoring at the last evaluable tumor assessment for participants without progression or death. The record does not provide additional details on missing assessments, follow-up completeness, or the statistical method used to calculate the fixed-time rate. Those gaps limit assessment of how censoring and unavailable outcome information affect the estimates.

The record lists many secondary outcomes but reports no secondary analyses. It does not explain multiplicity handling or the status of the 1-year objective described in the brief summary relative to the listed primary endpoint at 6 months. Subgroup and later follow-up results therefore require particular caution. Finally, these results concern a population that had received prior nivolumab and should not be assumed to describe populations or treatment settings not represented by the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Dose Frequency Optimization,Trial of Nivolumab 240 mg Every 2 Weeks vs Nivolumab 480 mg Every 4 Weeks in Subjects With Advanced or Metastatic Non-small Cell Lung Cancer Who Received Up to 12 Months of Nivolumab at 3 mg/kg or 240 mg Every 2 Weeks — NCT02713867.
• Registry record last updated 2023-02-14; status last verified 2023-01.
• Results first posted 2020-06-22.
• 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.

22. Record Summary

The registry record describes a completed randomized, unmasked, parallel-group comparison of nivolumab 480 mg every 4 weeks and nivolumab 240 mg every 2 weeks in advanced or metastatic non-small cell lung cancer. Participants had received up to 12 months of nivolumab before randomization. The primary outcome is progression-free survival rate at 6 months among all randomized participants.

The posted arm-level primary rates are 0.76 and 0.79, with 95% confidence intervals of 0.70 to 0.83 and 0.73 to 0.85, respectively. The listed comparison statistics do not appear consistent with those arm-level rates, and the registry record reports no analysis that resolves the mismatch. Original design assumptions, a full analysis plan, and multiplicity methods are not reported.

The secondary outcomes and serious adverse-event summaries provide additional descriptive information, but the record reports no secondary analyses. The posted data support cautious description of the trial outcomes, not a conclusion of equivalence or a treatment recommendation.