Nivolumab With or Without Ipilimumab in Treating Patients With Metastatic Sarcoma That Cannot Be Removed by Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nivolumab With or Without Ipilimumab in Treating Patients With Metastatic Sarcoma That Cannot Be Removed by Surgery (NCT02500797), a randomized phase 2 study. The primary outcome is Number of Participants Who Achieved a Confirmed Response.

2. Clinical Question

3. Trial Design

This was a randomized phase II study sponsored by the National Cancer Institute (NCI). The registry describes an open-label design with no masking and a crossover model. Its official title identifies the study as a randomized phase II study of nivolumab with or without ipilimumab in patients with metastatic or unresectable sarcoma. The registry lists enrollment as 164 and the status as completed. The recorded start date is 2015-08-13, and the primary completion date is 2019-04-01.

The two main regimens differed in the use of ipilimumab alongside nivolumab. In the single-agent arm, nivolumab was administered intravenously every 2 weeks, with cycles repeating every 42 days for up to 108 weeks if disease progression or unacceptable toxicity did not occur. Participants who progressed after 10 weeks on nivolumab alone could elect to cross over. In the combination arm, nivolumab and ipilimumab were administered every 3 weeks for 12 weeks, followed by nivolumab every 2 weeks. The registry describes the expansion cohorts as single-agent or combination treatment for LPS, UPS/MFH, and GIST.

The primary outcome timeframe is listed as up to 44 months. The endpoint population is described as participants who completed the study and were evaluable for the primary endpoint, rather than everyone enrolled. The record does not report the original statistical design assumptions or explain how participants were allocated among all the cohorts. Although the registry calls the overall design crossover, it does not provide separate outcomes after crossover or establish how crossover was handled in the reported comparisons. Thus, the initial randomized comparison and the expansion-cohort comparisons need to be interpreted in their own reported groups, without assuming that they represent one common analysis population.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: GIST Cohort: 24 patients assessed for eligibility; 3 excluded (i.e. ineligible) and 21 randomized.\> LPS Cohort: 37 patients assessed for eligibility; 11 excluded, 3 included (2 pre-registered as UPS/MFH cohort, 1 pre-registered as GIST cohort) and 29 randomized.\> UPS/MFH Cohort: 47 patients assessed for eligibility; 18 excluded and 29 randomized.

Only the first 6 of 8 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants who completed the study and were evaluable for the primary endpoint are included in this 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: Randomized patients are included in this analysis.

Only the first 6 of 9 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Who Achieved a Confirmed Response, measured over Up to 44 months.

The primary endpoint is a count of participants achieving a confirmed response. A response was defined as a best objective tumor status of complete response or partial response lasting at least 4 weeks, determined with RECIST v1.1. The registry describes complete response as disappearance of all evidence of disease and partial response as regression of measurable disease with no new sites. The timeframe was up to 44 months.

Response is a binary outcome at the participant level: each evaluable participant either met the stated response definition or did not. Reporting counts alongside the number evaluated allows the reader to see the event frequency in each arm. The risk difference expresses the absolute contrast between those frequencies, while a confidence interval communicates uncertainty around that contrast. These statistics describe the observed response data; they do not by themselves establish why a difference occurred or how it relates to outcomes not captured by this endpoint.

Using a confirmed response endpoint can provide a defined measure of tumor change, with confirmation intended to distinguish a response that persists from a single assessment. It is not the same as duration of response, progression-free survival, overall survival, or clinical benefit at 6 months. Those outcomes address different aspects of participants’ experience and are listed separately in the registry. The primary analysis was restricted to study completers who were evaluable, so its counts do not describe every enrolled participant. The registry record does not report further details about missing endpoint assessments or their handling.

7. Results Posted in the Registry

• Initial Dual: 14.3% (6/42) versus 4.8% (2/42) on control; risk difference 9.5 percentage points (95% CI -2.9 to 21.9), risk ratio 3.00 (0.64–14.02); unadjusted two-proportion z-test p = 0.137.
• LPS Single: 6.7% (1/15) versus 4.8% (2/42) on control; risk difference 1.9 percentage points (95% CI -12.3 to 16.1), risk ratio 1.40 (0.14–14.35); unadjusted two-proportion z-test p = 0.777.
• LPS Dual: 14.3% (2/14) versus 4.8% (2/42) on control; risk difference 9.5 percentage points (95% CI -9.9 to 29.0), risk ratio 3.00 (0.47–19.35); unadjusted two-proportion z-test p = 0.231.
• UPS/MFH Single: 7.7% (1/13) versus 4.8% (2/42) on control; risk difference 2.9 percentage points (95% CI -12.9 to 18.8), risk ratio 1.62 (0.16–16.41); unadjusted two-proportion z-test p = 0.684.

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.

6-Month Clinical Benefit Rate [Initial Cohort]

• 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:
  • Initial Dual: 11.9% (5/42) versus 9.5% (4/42) on control; risk difference 2.4 percentage points (95% CI -10.8 to 15.6), risk ratio 1.25 (0.36–4.33); unadjusted two-proportion z-test p = 0.724.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Initial Dual and the control. The interval gives the range of effects that remain compatible with the data.

6-Month Clinical Benefit Rate [Expansion LPS and UPS/MFH Cohorts Only]

• 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:
  • LPS Dual: 35.7% (5/14) versus 6.7% (1/15) on control; risk difference 29.0 percentage points (95% CI 1.0 to 57.1), risk ratio 5.36 (0.71–40.37); unadjusted two-proportion z-test p = 0.054.
  • UPS/MFH Single: 15.4% (2/13) versus 6.7% (1/15) on control; risk difference 8.7 percentage points (95% CI -14.6 to 32.0), risk ratio 2.31 (0.24–22.62); unadjusted two-proportion z-test p = 0.457.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LPS Dual and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between UPS/MFH Single and the control. The interval gives the range of effects that remain compatible with the data.

6-Month Clinical Benefit Rate [Expansion GIST Cohort Only]

• 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:
  • GIST Dual: 54.5% (6/11) versus 10.0% (1/10) on control; risk difference 44.5 percentage points (95% CI 9.7 to 79.4), risk ratio 5.45 (0.79–37.81); unadjusted two-proportion z-test p = 0.031.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for GIST Dual than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span clinical benefit at 6 months, duration of response, progression-free survival, overall survival, and adverse events. The numeric secondary efficacy results posted in the registry cover the 6-month clinical-benefit rates in the initial cohort and the LPS, UPS/MFH, and GIST expansion cohorts. These comparisons do not all point to the same degree of separation, and their precision varies. The record does not report numerical results for duration of response, progression-free survival, or overall survival in the material analyzed.

Clinical benefit at 6 months is not interchangeable with confirmed response. It is a separate endpoint at a specified time, and its observed pattern can differ from a response count accumulated over the primary endpoint timeframe. Thus, the secondary results can add context, but they cannot replace the primary endpoint or be treated as independent confirmation of it. Results from expansion cohorts also do not automatically generalize to the initial randomized population or to all sarcoma types.

The registry lists no reported analyses for these secondary outcomes. The comparisons that are present are unadjusted, and the record does not describe a prespecified order for testing them or an adjustment for multiple comparisons. When many outcomes and cohorts are examined, an isolated result may appear noteworthy even if the broader evidence is uncertain. Secondary results are therefore best read as exploratory or descriptive unless the registry records a confirmatory analysis plan and interpretation.

In combination, the secondary outcome listings show the breadth of outcomes the study intended to assess, but the available numerical results do not offer a complete account of that breadth. They should be considered alongside the primary response comparison, with attention to endpoint differences, cohort size, interval width, and the absence of reported multiplicity handling. No overall conclusion across all secondary outcomes can be drawn from outcomes for which results are not reported.

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

• Number of Participants Who Experienced at Least One Grade 3 or Higher Adverse Event Regardless of Attribution
• Duration of Response
• 6-Month Clinical Benefit Rate [Initial Cohort]
• 6-Month Clinical Benefit Rate [Expansion LPS and UPS/MFH Cohorts Only]
• 6-Month Clinical Benefit Rate [Expansion GIST Cohort Only]
• Progression-free Survival (PFS)
• Overall Survival (OS)

9. Statistical Interpretation

10. Statistical Methods Explained

The reported outcomes include participant counts and percentages, with unadjusted comparisons between arms. The methods below explain how to read those statistics in general; they do not describe an unreported analysis plan for the study. The registry record does not report the original statistical plan, including whether any particular tests or adjustment procedures were prespecified.

What does a risk difference describe?

A risk difference is the event frequency in one group minus the event frequency in the comparator group. For this binary endpoint, the event is a confirmed response. A positive estimate indicates that the observed response frequency is higher in the named arm; a negative estimate indicates that it is lower. The risk difference is an absolute contrast, rather than a relative measure. It keeps the comparison tied to the observed frequency of the event in the groups being compared.

The primary comparison gives the risk difference as 0.095. The interval around it includes negative and positive values, so the posted data are compatible with a range of possible contrasts. A point estimate is only the center of an estimate, not a guarantee that the true effect equals that value. With small event counts, estimates can shift substantially when the observed count changes, and uncertainty should be read alongside the point estimate.

How should a p-value be read?

An unadjusted p-value is a measure of how unusual the observed data, or data more extreme, would be under a specified null model and test procedure. It is not the probability that the null hypothesis is true, nor the probability that the result arose “by chance.” A p-value also does not tell the reader whether a difference is clinically important. The p-value for the initial primary comparison is 0.137; the confidence interval is more informative about the range of contrasts compatible with the data.

“Unadjusted” means the reported comparison is not presented as corrected for the presence of other comparisons. Multiple testing can make isolated small p-values less persuasive because there are several opportunities to observe an apparently unusual result. A prespecified testing order or an adjustment can address some of that issue, but the registry record does not report such a plan for these results.

What does randomization contribute?

Random allocation is intended to make treatment groups comparable, on average, with respect to factors known and unknown at assignment. That rationale supports interpreting the initial comparison as a randomized comparison, but it does not remove uncertainty from sparse outcome data, missing endpoint observations, or departures from the assigned treatment. The registry labels the study randomized and unmasked. It does not report enough detail to assess allocation concealment, adherence, or how the analysis accounted for crossover.

The overall trial uses a crossover model, and participants assigned to nivolumab alone who progressed after 10 weeks could elect to cross over. A crossover can affect interpretation of outcomes occurring after the switch, especially time-to-event outcomes. The posted primary endpoint is a response count, but the record does not report separate post-crossover response results or the exact treatment-policy approach used in analysis. The initial arm-level counts should therefore be read as posted, not as a reanalysis that resolves crossover effects.

Why do the expansion cohorts need separate reading?

The registry reports LPS, UPS/MFH, and GIST cohorts as distinct sets of comparisons. Their event counts and arm sizes are small, so their intervals are wide and the estimates can be sensitive to a few outcomes. Differences among histologies may also matter to interpretation, but the record does not report a model that accounts for histology or tests whether effects vary by cohort. These subgroup-style results are descriptive evidence for the named groups rather than a precise estimate applicable to every sarcoma type.

For binary outcomes, the number with the event and the number evaluated are essential context. A percentage alone can obscure how little information underlies an estimate. Confidence intervals express sampling uncertainty, but they do not account for all sources of uncertainty, such as selection into an evaluable population, measurement issues, or multiplicity. Those issues require study-design and analysis details that are not reported in the registry record.

What can be inferred from the posted methods?

The primary result is reported as a count with arm-specific denominators and a risk-difference comparison. This makes the observed event frequencies and the absolute contrast readable. The reported p-values are explicitly unadjusted, and the confidence intervals give a range of estimates under the method used. The registry does not report details such as the exact confidence-interval construction, analysis population rules beyond study completion and endpoint evaluability, or a missing-data strategy. Consequently, the figures can be described, but their calculation cannot be fully audited from the registry record alone.

11. Confidence Intervals and Precision

A confidence interval describes uncertainty around an estimated contrast under the statistical method used. It is not a range that is guaranteed to contain the true value, nor does its width capture every uncertainty in the study. The interval for the initial primary risk difference is -0.029 to 0.219. It includes zero, which corresponds to no difference in observed response frequencies, and also includes contrasts in either direction. The point estimate, 0.095, should therefore not be read without the interval.

The small numbers of observed responses contribute to imprecision. In the initial arms, the posted counts are 2 of 42 and 6 of 42. A confidence interval around a binary outcome comparison reflects the limited information in those observed events. The expansion comparisons are based on still smaller cohorts and similarly few responses; their reported intervals are broad. In the GIST response comparison, there were no confirmed responses in either arm, so the posted comparison does not establish equivalence or rule out differences not captured by the observed sample.

Precision is distinct from whether a result passes a threshold for statistical significance. An interval can include no difference and still contain effects that might matter, in either direction. Conversely, a narrower interval would not by itself establish that an effect is clinically meaningful. The 6-month clinical-benefit endpoints report confidence intervals at different stated confidence levels across cohorts: 90% for the initial cohort, 85% for the LPS and UPS/MFH expansion cohorts, and 80% for GIST. Intervals at different confidence levels should not be compared as though they had identical coverage.

These intervals describe sampling uncertainty in the posted comparisons. They do not quantify uncertainty from endpoint-evaluable selection, crossover, unreported missing-data handling, or the many outcomes and comparisons. The registry record does not report enough detail to assess those additional sources fully.

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 illustrations translate an observed contrast into hypothetical future planning requirements; they are not the enrollment targets that governed this study. For the binary outcomes, the figures are participants per arm, not total participants across both arms and not total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column represents a planning scenario in which a study using the stated assumptions would have an 80% chance of detecting the specified effect if that effect were the true one. The 90% column represents a higher target probability under those same assumptions. Neither column tells how likely the observed study was to have detected an effect after its results were known. This is a planning illustration, not observed power.

Rows labeled as planning for 100%, 75%, or 50% of the observed effect use progressively smaller effects as the target to detect. Smaller effects generally require more participants to distinguish them from sampling variation under a fixed design and significance level. This explains why the planning figures increase as the assumed effect fraction decreases. The illustrations use the observed effect as their starting point, which can be uncertain when event counts are sparse. They therefore should not be treated as proof that a future study would attain the stated operating characteristics if its actual effect, population, or analysis differed from the assumptions.

Where a sample-size curve accompanies these figures, it should be read as the same planning relationship across candidate effect sizes: the required participants per arm depend on the target effect and desired power. The curves do not describe the actual power of the completed trial, provide a retrospective validation of its design, or substitute for the original protocol’s justification. The registry record does not report that 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

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 = 0.048; treatment proportion p₁ = 0.143; average p̄ = 0.095.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4151 = 0.8136.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4096 = 0.3448.
4. n = (0.8136 + 0.3448)² / (0.0952)² = 147.9, rounded up to 148 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 <- 0.0476190476190476                          # control proportion
p1 <- 0.142857142857143                          # 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(2500797)
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 = 148 (80% power), 198 (90% power)
 75% of observed effect: n per arm = 234 (80% power), 313 (90% power)
 50% of observed effect: n per arm = 458 (80% power), 613 (90% power)
power.prop.test: 147.9 
Simulated power at n = 148 per arm: 0.817 (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

Several outcomes and cohort-specific comparisons are listed, including the primary confirmed-response endpoint, clinical benefit at 6 months, duration of response, progression-free survival, overall survival, and adverse events. Examining multiple endpoints and treatment contrasts creates a multiplicity issue: even when no real treatment difference exists, some comparisons may look unusual by chance. This does not invalidate each estimate, but it changes how much weight should be placed on an isolated unadjusted p-value.

The registry record does not report a multiplicity adjustment, a hierarchical testing sequence, or which secondary results were intended to be confirmatory. The posted comparison p-values are unadjusted. Without a stated plan, the reader cannot determine whether the primary endpoint was the only formal test, how secondary endpoints were to be interpreted, or whether cohort-specific results were planned as separate hypotheses. These details are not reported in the registry record.

The record says that participants who completed the study and were evaluable for the primary endpoint are included in that analysis. It does not report how many enrolled participants were excluded from the primary endpoint analysis, why they were not evaluable, or how missing response assessments were handled. It also does not describe whether missing outcomes were treated as non-response, excluded, or addressed by another method. The arm-level denominators in the posted results should not be assumed to represent every randomized participant.

Analysis-population details are limited. The registry does not report a full intention-to-treat analysis, a per-protocol analysis, or a sensitivity analysis for missing data. Because the design includes optional crossover after progression, the record’s lack of a reported crossover analysis also limits interpretation of outcomes that could be affected by treatment switching. These gaps do not change the reported counts, but they constrain assessment of robustness and of how closely the analyses reflect random assignment.

These missing details matter because multiplicity, participant exclusions, missing observations, and crossover can influence interpretation in different ways. The record supports describing the posted estimates and their stated uncertainty; it does not support reconstructing an unreported analysis plan or determining whether the results were adjusted for all planned comparisons.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diarrhea (27.3%), fever (15.4%), anemia (13.3%), fatigue (13.3%), small intestinal obstruction (10.0%).

The registry reports counts of participants affected by at least one serious adverse event within each listed group. For example, the initial single-agent group reports 19 of 42, and the initial combination group reports 21 of 42. The expansion groups are reported separately, with their own numbers at risk and affected. These are participant counts, not counts of individual event episodes. A participant with more than one event may still contribute once to the count of participants affected.

The registry also lists common serious-event terms and percentages, including diarrhea at 27.3%, fever at 15.4%, anemia at 13.3%, fatigue at 13.3%, small intestinal obstruction at 10.0%, and vomiting at 10.0%. The record does not provide enough context in these figures alone to infer attribution to study treatment or compare the overall safety of regimens. Serious adverse events are not necessarily equivalent to the separately listed secondary outcome of grade 3 or higher adverse events regardless of attribution. The posted safety counts should be read as descriptive, with the group denominators and endpoint definitions in mind.

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

The primary result describes confirmed responses observed among participants who completed the study and were evaluable for the endpoint. In the initial cohort, the combination arm had more observed responses than the nivolumab-alone arm, and the estimated absolute difference favored the combination. The confidence interval is wide and includes no difference, however, so the estimate is not precise enough to establish a clear contrast from these data alone. The result is an estimate with uncertainty, not a definitive statement about the comparative effect.

The data do not show that the regimens are equivalent. A non-significant unadjusted comparison does not prove that there is no difference; it indicates that the observed data do not clearly distinguish the contrast from no difference under the reported analysis. Similarly, the point estimate favoring the combination does not by itself prove a benefit. Both direction and magnitude remain uncertain, particularly given the small number of observed responses.

The expansion cohort outcomes are specific to the reported histology groups and have their own small denominators and uncertainty. They do not establish a treatment effect across all sarcomas. The clinical-benefit endpoint is distinct from confirmed response, and the registry record does not report results for several other listed secondary outcomes. Consequently, the available results cannot support a comprehensive conclusion about tumor control, survival, or the balance between efficacy and harms.

Safety counts also require careful interpretation. They describe participants recorded as having serious adverse events, but the figures do not establish that events were caused by a treatment. The registry lists adverse events regardless of attribution as another outcome, and serious adverse events and grade 3 or higher events are not interchangeable categories. The reported data should not be treated as individualized predictions or medical guidance.

In short, the record documents the study design and the posted outcome counts, but it does not resolve whether adding ipilimumab changes confirmed response in the initial cohort. It also does not answer all questions about longer-term outcomes, crossover, missing data, or multiplicity. Readers should distinguish what was observed in these groups from broader claims that the registry results do not establish.

17. Why This Trial Matters Statistically

This study presents a useful statistical example of how a randomized comparison can still yield an uncertain estimate when the endpoint is observed infrequently. The primary outcome is easy to define and interpret as a participant-level response, yet the small event counts leave a broad range of plausible contrasts. The central lesson is that an estimated direction and a precise conclusion are not the same thing.

The record also separates an initial randomized comparison from histology-specific expansion cohorts. Such reporting makes clear that an apparent pattern in one group should not automatically be generalized to another. The cohort-specific findings invite questions about whether effects vary across sarcoma types, but the registry record does not report a formal interaction analysis or a pooled model. Statistical discipline means preserving those distinctions rather than combining groups informally.

Another important issue is the difference between endpoints. Confirmed response, 6-month clinical benefit, progression-free survival, overall survival, and adverse events address different questions. A pattern in one endpoint cannot be assumed to recur in another. Where outcomes are listed but their numerical results are not reported, the correct interpretation is that the registry record does not report them, not that they showed no effect.

Finally, the posted unadjusted comparisons occur among multiple outcomes and cohorts, while details about multiplicity, missing data, and crossover handling are absent. This illustrates why p-values should be read with effect estimates, confidence intervals, endpoint definitions, and analysis-population information. Together, these statistical considerations show why transparent reporting of both estimates and analysis choices is essential for interpreting a clinical trial.

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.

The response analysis applies to participants who completed the study and were evaluable for the primary endpoint. The registry does not report the number of otherwise enrolled or randomized participants who were not included in that endpoint analysis, reasons for exclusion, or how missing assessments were handled. This limits assessment of whether the evaluable population remained comparable to the randomized groups.

The overall design allowed optional crossover from nivolumab alone to the combination after progression at the stated time. The registry does not report how many participants crossed over, when they did so, or how the primary and secondary analyses treated the switch. This is especially relevant to outcomes measured over time, but the record does not provide enough detail to evaluate its impact.

The expansion cohorts report small, separate groups for LPS, UPS/MFH, and GIST. Their estimates are imprecise, and the registry does not report a statistical model for comparing effects across histologies or an overall pooled analysis. The results should therefore not be generalized beyond the cohorts and comparisons described.

The registry record does not report the trial’s original sample-size justification, detailed statistical analysis plan, multiplicity strategy, or full methods for constructing the reported intervals. It also lists duration of response, progression-free survival, and overall survival without numerical results in the posted material. These reporting gaps limit independent assessment of planned versus reported analyses and of the breadth of outcome evidence.

The study was unmasked, and the registry does not provide additional details about outcome assessment procedures beyond the RECIST v1.1 response definition. These limitations do not negate the reported observations, but they restrict how confidently the comparisons can be interpreted beyond their descriptive estimates.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Nivolumab With or Without Ipilimumab in Treating Patients With Metastatic Sarcoma That Cannot Be Removed by Surgery — NCT02500797.
• Registry record last updated 2023-10-17; status last verified 2023-09.
• Results first posted 2020-06-16.
• 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 describes a completed, randomized, unmasked phase II study comparing nivolumab alone with nivolumab plus ipilimumab in metastatic or unresectable sarcoma. The primary endpoint counted confirmed complete or partial responses lasting at least 4 weeks. In the initial cohort, the combination arm had 6 responses among 42 participants and the single-agent arm had 2 among 42; the unadjusted risk difference was 0.095, with a 95% confidence interval from -0.029 to 0.219.

The record also reports 6-month clinical-benefit results in the initial and expansion cohorts, and descriptive serious adverse-event counts. Several listed secondary outcomes have no numerical results in the registry record. The available primary estimate favors the combination in direction but is imprecise and includes no difference. Missing details about multiplicity, missing data, crossover handling, and the original design assumptions further limit interpretation.