To Evaluate the Efficacy and Safety of Parsaclisib and Ruxolitinib in Participants With Myelofibrosis (LIMBER-313): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Evaluate the Efficacy and Safety of Parsaclisib and Ruxolitinib in Participants With Myelofibrosis (LIMBER-313) (NCT04551066), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving ≥35% Reduction in Spleen Volume From Baseline to Week 24 as Measured by Magnetic Resonance Imaging [MRI] (or Computed Tomography [CT] Scan in Applicable Participants).

2. Clinical Question

The clinical question is whether the combination containing parsaclisib differs from ruxolitinib with placebo on this defined imaging outcome. The endpoint compares each participant’s spleen volume at baseline with the Week 24 measurement, then classifies whether the specified reduction was reached. The registry reports the endpoint as a percentage of participants, so the principal result is a comparison of event proportions rather than an average change in spleen volume.

The record also lists symptom-score outcomes, overall survival, and safety outcomes. Those measures provide additional context, but they do not replace the primary question. The study is listed as terminated; the reason for termination is not reported in the registry record. The registry record does not establish why the study ended or what decision followed from the posted result.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study. The record describes triple masking, but does not report which roles or groups were masked. The planned comparison was parsaclisib plus ruxolitinib against placebo plus ruxolitinib, with allocation determined by randomization. The listed enrollment was 252 participants.

The study began on 2021-05-24, and the primary completion date is listed as 2023-08-03. Its status is terminated. The registry record does not report the reason for termination, whether the listed enrollment was fully randomized, or whether the primary completion date reflects the timing of all follow-up and analysis.

The primary endpoint population is described as the intent-to-treat population, meaning all randomized participants, with treatment groups defined by randomized assignment regardless of the study drug actually taken. The posted primary endpoint arm denominators are 89 for parsaclisib plus ruxolitinib and 92 for placebo plus ruxolitinib. These are smaller than the listed enrollment; the registry record does not explain the difference. Safety outcomes use denominators of 125 and 127, respectively, so they should be read as a separate set of posted safety counts rather than as the primary endpoint denominators.

Ruxolitinib was given in both groups, and the described dose depended on baseline platelet count. The study therefore tests the addition of parsaclisib relative to adding placebo to ruxolitinib; it is not a comparison of parsaclisib alone with no active treatment. The original protocol’s sample-size justification, target effect, randomization details beyond the parallel randomized design, and other design assumptions are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: This study was conducted at 93 study sites in Austria, Belgium, China, Denmark, Finland, France, Germany, Israel, Italy, Japan, Norway, Poland, South Korea, Spain, Turkey, the United Kingdom, and the United States.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all randomized participants. Treatment groups were defined according to the treatment assignment at randomization regardless of the actual study drug the participant took during their participation. Participants who had both Baseline and Week 24 measurements, or discontinued treatment before 27APR2023, or reached Week 24 before 27APR2023 but were missing Week 24 assessments were analyzed.

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 Percentage of Participants Achieving ≥35% Reduction in Spleen Volume From Baseline to Week 24 as Measured by Magnetic Resonance Imaging [MRI] (or Computed Tomography [CT] Scan in Applicable Participants), measured over Baseline; Week 24.

The primary endpoint is the percentage of participants achieving at least a 35% reduction in spleen volume from baseline to Week 24. Spleen volume was assessed by MRI; a CT scan was substituted when a participant was not a candidate for MRI or when MRI was not readily available. The registry description also mentions palpation with a flexible ruler to measure spleen length below the left costal margin, but the primary outcome itself is defined by imaging-based spleen volume.

This is a binary endpoint: each participant either reaches the stated reduction threshold or does not. The arm-level percentage summarizes how frequently that event occurred. It does not describe the size of the reduction among participants who reached the threshold, nor does it show the distribution of individual spleen-volume changes.

General statistical context: a threshold-based endpoint can make a result straightforward to interpret as the proportion reaching a prespecified criterion, but it also discards information about changes that fall on either side of the threshold. Participants with different degrees of change can be counted alike if they both meet the criterion, while a small difference around the cutoff can place otherwise similar measurements into different categories. The registry uses this measure to compare the two randomized groups at Week 24. The reason this particular threshold was selected, and the protocol’s rationale for choosing it as the primary endpoint, are not reported in the registry record.

7. Results Posted in the Registry

• Parsaclisib Plus Ruxolitinib: 52.8% (47/89) versus 46.7% (43/92) on control; risk difference 6.1 percentage points (95% CI -8.5 to 20.6), risk ratio 1.13 (0.84–1.52); unadjusted two-proportion z-test p = 0.414.

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.

Percentage of Participants Who Had a ≥50% Reduction in Total Symptom Score (TSS) From Baseline to Week 24 as Measured by the Myelofibrosis Symptom Assessment Form v4.0 (MFSAF v4.0) Diary

• 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:
  • Parsaclisib Plus Ruxolitinib: 34.8% (31/89) versus 38.8% (38/98) on control; risk difference -3.9 percentage points (95% CI -17.8 to 9.9), risk ratio 0.90 (0.62–1.31); unadjusted two-proportion z-test p = 0.577.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Parsaclisib Plus Ruxolitinib and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Any Grade 3 or Higher TEAE

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Parsaclisib Plus Ruxolitinib: 60.0% (75/125) versus 59.1% (75/127) on control; risk difference 0.9 percentage points (95% CI -11.2 to 13.1), risk ratio 1.02 (0.83–1.25); unadjusted two-proportion z-test p = 0.879.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Parsaclisib Plus Ruxolitinib and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning symptom response and change, time to symptom response, overall survival, and treatment-emergent adverse events. The numerical results cover a subset of that range, including the symptom-response threshold and Grade 3 or higher treatment-emergent adverse events. The posted symptom-response percentages do not show a pattern that clearly reinforces the primary endpoint’s apparent direction, while the Grade 3 or higher event counts are similar across the two reported safety groups. This broad description should not be mistaken for a formal joint assessment of all secondary outcomes.

Secondary measures can help describe whether a primary result is accompanied by patterns in symptoms, survival, or safety. They do not automatically confirm or overturn the primary finding. Different outcomes have different definitions, follow-up periods, analysis populations, and sources of uncertainty. In particular, symptom-based measures are distinct from an imaging-based spleen-volume endpoint, so agreement is not guaranteed even when both are measured in the same study.

Unadjusted secondary analyses carry less weight for confirmatory claims when many outcomes are examined. General statistical context: as the number of tests increases, the chance of at least one apparently notable result arising by chance also increases unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy for testing the secondary outcomes. It also does not report numerical results for every listed secondary outcome in the results. The available secondary findings should therefore be treated as supportive description rather than independent proof of a treatment effect.

For the primary result, the sponsor’s confidence interval includes the no-difference value. Secondary endpoints do not resolve that uncertainty on their own, particularly when the full testing strategy and analysis details are not reported. The registry record does not establish a consistent overall pattern across all listed outcomes.

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

• Percentage of Participants Who Had a ≥50% Reduction in Total Symptom Score (TSS) From Baseline to Week 24 as Measured by the Myelofibrosis Symptom Assessment Form v4.0 (MFSAF v4.0) Diary
• Change in TSS From Baseline to Week 24 as Measured by the MFSAF v4.0 Diary
• Time to the First ≥50% Reduction in TSS as Measured by the MFSAF v4.0 Diary
• Overall Survival
• Number of Participants With Any Treatment-emergent Adverse Event (TEAE)
• Number of Participants With Any Grade 3 or Higher TEAE
• Time of Onset of a ≥35% Reduction in Spleen Volume
• Duration of Maintenance of a ≥35% Reduction in Spleen Volume

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant achieved the defined reduction threshold by Week 24. For a binary outcome, an arm-level percentage is the proportion of participants with the event among those represented in that arm’s analysis. A comparison can then be expressed in different ways. The risk difference compares the two proportions directly, whereas an odds ratio compares the odds of the event between groups. These measures answer related but not identical questions and are not numerically interchangeable.

The recalculated result on this page is an unadjusted risk-difference comparison using the posted arm summaries. “Unadjusted” means that the calculation does not account for additional variables or strata. It is a simple re-calculation from the posted summary data, not a replacement for the study’s own statistical analysis. Its confidence interval describes uncertainty around that unadjusted contrast under the calculation’s assumptions.

The sponsor reported a Cochran-Mantel-Haenszel analysis of the primary endpoint, with an odds ratio as the effect measure. In general, the Cochran-Mantel-Haenszel method combines information across strata to estimate an association while accounting for stratification. The specific stratification factors and implementation details are not reported in the registry record, so the analysis cannot be reconstructed fully from the posted summary. The sponsor’s reported odds ratio and confidence interval should be distinguished from the unadjusted risk difference shown in the recalculation.

General statistical context: an odds ratio of 1 represents equal odds in the two groups, while an odds ratio above or below 1 indicates a relative direction in the coded comparison. For a confidence interval around an odds ratio, including 1 means that the range of estimates is compatible with no odds difference as well as with effects in either direction. For a risk difference, the corresponding no-difference value is zero. The sponsor’s interval includes 1; the recalculated interval includes zero. Neither interval alone gives the probability that a particular effect is true.

A p-value summarizes how unusual data at least as incompatible with a null hypothesis would be under that null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an effect. The registry reports p-values for the primary and some secondary outcomes. The interpretation relies on the effect estimates and their confidence intervals rather than treating a p-value as a stand-alone decision.

Randomization is intended to make the treatment groups comparable on average, including with respect to factors that are measured and factors that are not. Blinding can limit some influences on care, assessment, and reporting, depending on who is masked and how the masking is maintained. This record identifies a randomized, double-blind, placebo-controlled design and triple masking, but does not identify the masked roles or provide enough detail to assess the implementation.

The primary population is defined as all randomized participants, grouped according to assignment regardless of the actual study drug taken. This intent-to-treat definition preserves the randomized comparison in principle. However, the posted endpoint denominators are smaller than the listed enrollment, and the endpoint population text in the registry record is incomplete. The handling of missing measurements, exclusions, and any imputation is not reported in the registry record. As a result, the posted summaries do not show how much the analysis may depend on the availability of Week 24 imaging.

The registry lists secondary outcomes including symptom response, change in symptom score, time to symptom response, overall survival, and adverse events. A result for an outcome is not automatically confirmatory simply because it appears in a registry. Statistical interpretation also depends on whether the endpoint and analysis were prespecified, whether comparisons were adjusted for multiple testing, and how missing observations and censoring were handled. Those details are not reported for the secondary analyses in this record.

General statistical context: over-dispersion is relevant when count data vary more than a statistical model expects. A model that assumes less variability than is present can produce uncertainty estimates that are too narrow. The primary endpoint is a participant-level binary outcome rather than a count of repeated events, so a discussion of over-dispersion is not central to the posted primary comparison. For time-to-event outcomes, methods also need to account for follow-up time and censoring; the registry lists overall survival and time-to-event symptom outcomes, but their analysis methods are not reported in the available results.

11. Confidence Intervals and Precision

The sponsor’s primary analysis gives an odds ratio of 1.27 with a 95% confidence interval from 0.71 to 2.26. This is a wide interval that spans values on either side of 1. It is compatible with lower odds, no odds difference, or higher odds for the parsaclisib-plus-ruxolitinib group under the reported comparison. The interval therefore conveys substantial uncertainty about the magnitude and direction of the association.

General statistical context: a confidence interval is a range produced by a method designed to cover the underlying effect at its stated confidence level over repeated use of that method, assuming the analysis model and data conditions are appropriate. It is not a range containing a fixed percentage of individual participant outcomes, and it is not a probability statement that the true effect lies inside this particular interval. The confidence level does not remove uncertainty about analysis choices, missing data, or potential limitations in the record.

The arm percentages are based on 89 and 92 participants, and the interval reflects the uncertainty associated with the study’s posted comparison. The registry’s recalculated risk-difference interval also includes no difference. The figures do not precisely establish how large any difference might be. The fact that the point estimate favors one direction does not erase the uncertainty shown by the interval, and the interval does not prove equivalence between the groups.

The record does not report a prespecified precision target or the original sample-size justification, so it is not possible to judge the observed interval against the trial’s intended precision. The posted enrollment and the smaller primary endpoint denominators also make it important to keep the analyzed outcome data distinct from the overall enrollment. The record does not explain the denominator difference or the extent and handling of missing endpoint measurements.

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 table is a planning illustration based on the observed effect, not the trial’s original design calculation. Its entries for this binary endpoint are participants per arm, not total participants and not 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 effect to detect is the stated fraction of the observed effect. The trial’s original sample-size assumptions are not reported in the registry record.

For the full observed effect, the illustration gives 1,064 participants per arm for 80% power and 1,424 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 1,892 participants per arm for 80% power and 2,532 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 4,255 participants per arm for 80% power and 5,695 participants per arm for 90% power.

In plain terms, the 80% power column describes a planned sample size that, under the stated assumptions and effect size, would give the test an 80% chance of detecting that effect at the specified significance level if the effect were present. The 90% column uses a higher chance of detection and therefore requires more participants in these illustrations. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants. These figures are not observed power; they are planning illustrations and should not be read as evidence about the chance that this completed study detected an effect.

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 = 0.467; treatment proportion p₁ = 0.528; average p̄ = 0.498.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3859.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7058 = 0.5940.
4. n = (1.3859 + 0.5940)² / (0.0607)² = 1,064.0, rounded up to 1,064 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 <- 0.467391304347826                          # control proportion
p1 <- 0.528089887640449                          # 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(4551066)
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 = 1,064 (80% power), 1,424 (90% power)
 75% of observed effect: n per arm = 1,892 (80% power), 2,532 (90% power)
 50% of observed effect: n per arm = 4,255 (80% power), 5,695 (90% power)
power.prop.test: 1064 
Simulated power at n = 1,064 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. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analysis is a Cochran-Mantel-Haenszel odds-ratio analysis. It reports an odds ratio of 1.27, a 95% confidence interval from 0.71 to 2.26, and a p-value. The interval includes the no-difference value for an odds ratio, so the reported analysis does not establish a clear difference between groups.

The recalculation shown alongside it uses an unadjusted risk difference derived from posted arm summaries. The risk difference is a direct contrast between event proportions, while the sponsor’s odds ratio compares odds and uses a stratified method. Because these are different effect measures and analytical approaches, their estimates should not be treated as duplicate versions of the same number. The recalculation is useful as a transparent check on the posted group summaries, but it does not supersede the sponsor’s own analysis.

The registry does not flag a discrepancy between the recalculation and the sponsor-reported analysis. Details of the sponsor analysis’s strata and full statistical specification are not reported in the registry record. The sponsor result is therefore the principal reported inferential result, while the recalculation offers a separate, unadjusted description of the contrast.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and multiple secondary outcomes, but does not report a multiplicity-control strategy, a formal testing hierarchy, or which secondary comparisons, if any, were intended to support confirmatory claims. When several outcomes are tested, interpreting each p-value as if it were the only test can overstate the strength of evidence. General statistical context: multiplicity procedures are designed to control the overall risk of false-positive conclusions across a set of tests. Without a reported strategy, secondary p-values should be interpreted cautiously, and a nominal result should not be treated as definitive evidence.

The primary endpoint population is described as intent-to-treat, with participants grouped according to randomized assignment. The accompanying description is truncated after starting to qualify which participants had baseline and Week 24 measurements. The registry record does not report the missing-data method, the number of participants without endpoint measurements, reasons for missingness, or whether any sensitivity analyses were conducted. It is therefore not possible to assess from the record whether the missing-data assumptions are plausible or how alternative assumptions might affect the primary comparison.

The endpoint arm denominators differ from the listed enrollment, and the safety denominators differ from the primary endpoint denominators. These differences may reflect distinct analysis sets or availability requirements, but their explanation is not reported in the registry record. No reason should be inferred from the counts alone.

The record identifies the primary population as intent-to-treat, but does not provide complete analysis-population definitions for all outcomes. It does not report the handling of treatment discontinuation, protocol deviations, censoring for time-to-event outcomes, or missing symptom diaries. These are relevant to interpreting outcomes such as overall survival and time to symptom response. The registry record also does not provide the original statistical analysis plan, so the prespecified methods and any planned sensitivity analyses cannot be verified.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaemia (3.2%), pneumonia (3.2%), pancreatitis acute (2.4%), pneumocystis jirovecii pneumonia (1.6%), pulmonary embolism (1.6%).

The registry reports serious adverse events in 26 of 125 participants in the parsaclisib-plus-ruxolitinib safety group and 18 of 127 participants in the placebo-plus-ruxolitinib group. The record lists deaths as 6 and 3, respectively. These are descriptive counts in the posted safety data; they do not by themselves establish that treatment caused an event or death. A participant-level count also does not convey event timing, duration, severity beyond the category reported, or the full clinical context.

The registry identifies anaemia and pneumonia as the most frequently listed serious-event terms, each reported as 3.2% in the posted safety record, followed by acute pancreatitis, Pneumocystis jirovecii pneumonia, pulmonary embolism, and atrial fibrillation at the listed percentages. These entries describe the recorded terms and frequencies; they are not a complete account of all adverse events. The record also lists 75 participants with a Grade 3 or higher treatment-emergent adverse event in each group, using denominators of 125 and 127.

General statistical context: safety comparisons need to be read with attention to exposure duration, event definitions, and how events were collected. Those details are not fully. The registry figures support description of the reported counts, but not a causal safety conclusion or a comprehensive comparison of risk.

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

The posted results show that the Week 24 spleen-volume reduction threshold was reached by 52.8% of participants in the parsaclisib-plus-ruxolitinib arm and 46.7% in the placebo-plus-ruxolitinib arm. The sponsor’s odds-ratio estimate is 1.27, with a 95% confidence interval from 0.71 to 2.26. Because that interval includes 1, the reported analysis does not provide clear statistical evidence of a difference between the groups.

This does not show that the groups are equivalent. A result that does not establish a difference can reflect an effect that is small, uncertain, or estimated imprecisely; the interval remains compatible with effects in either direction. The confidence interval does not establish that the treatment has no effect, nor does the point estimate alone prove that it has an effect. The posted comparison is a statistical summary, not a conclusion about an individual participant.

The result also does not establish how treatment affects symptoms, survival, or all aspects of safety. The registry lists outcomes in those domains, but the available numerical results and analysis details are incomplete. The study’s termination status does not explain the reason for stopping, and the registry record does not establish whether termination was related to efficacy, safety, recruitment, or another consideration.

General context: a randomized comparison can inform an average contrast between groups as studied, but its interpretation depends on outcome measurement, follow-up, missing data, and the analysis plan. Here, the primary endpoint was a threshold-based imaging measure at Week 24. It does not summarize every possible patient experience or longer-term outcome. The appropriate conclusion is limited to the posted endpoint estimates and their uncertainty; the record does not support a broader claim that either regimen works or does not work.

18. Why This Trial Matters Statistically

This study is statistically informative because it compares adding parsaclisib with adding placebo while ruxolitinib is used in both groups. That design makes the primary contrast relevant to the additional treatment component rather than a comparison of two wholly different treatment strategies. Randomization and masking are important design features, although the registry does not specify who was masked or give enough detail to assess implementation.

The primary outcome is a clearly defined threshold on spleen-volume change, assessed with imaging at baseline and Week 24. The result can therefore be read as the proportion reaching a stated endpoint. At the same time, the confidence interval is broad and includes the no-difference value in the sponsor analysis. This illustrates why an arm-level percentage or a favorable point estimate is not enough: uncertainty and the analysis method are central to interpretation.

The record also demonstrates the distinction between an adjusted or stratified sponsor analysis and an unadjusted recalculation from group summaries. Each has a different role. The sponsor analysis is the reported inferential result; the recalculation helps readers understand the contrast in a simpler form, but does not reproduce every aspect of the sponsor’s method.

Finally, the termination status, denominator differences, and incomplete reporting of missing-data and multiplicity methods matter when assessing how much can be concluded. These gaps do not negate the posted results, but they limit independent evaluation of the full trial analysis. The case is a useful example of reading a clinical-trial result as a combination of design, endpoint, estimate, uncertainty, and reporting completeness rather than as a single percentage.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations restrict interpretation of the registry results. First, the listed enrollment is 252, while the primary endpoint denominators are 89 and 92. The record does not explain this difference or fully describe how participants with unavailable Week 24 measurements were handled. The safety denominators are 125 and 127, so safety and efficacy summaries refer to different posted group sizes.

Second, the primary endpoint population description is incomplete in the registry record. Although it identifies the intent-to-treat population, it ends while describing measurement availability. The record does not report missing-data procedures or sensitivity analyses. This makes it difficult to assess the influence of missing endpoint observations.

Third, the sponsor reports a stratified odds-ratio analysis, but the factors used for stratification and further implementation details are not reported. The recalculated risk difference is unadjusted and is not a substitute for the full sponsor analysis. The original statistical analysis plan and original sample-size justification are also not reported.

Fourth, the record lists several secondary outcomes but does not report a multiplicity strategy or a complete set of numerical secondary results. It also does not provide full analysis details for time-to-event outcomes, symptom diaries, or safety follow-up. These gaps limit the strength of conclusions drawn across outcomes.

Finally, the study is listed as terminated, but the reason is not reported in the registry record. The listed dates and status alone do not establish whether or why the study ended earlier than planned, or whether termination affected follow-up or analysis. These limitations are specific to what can be evaluated from the registry record and should not be filled in by assumption.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: To Evaluate the Efficacy and Safety of Parsaclisib and Ruxolitinib in Participants With Myelofibrosis (LIMBER-313) — NCT04551066.
• Registry record last updated 2025-10-21; status last verified 2025-09.
• Results first posted 2024-10-04.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

LIMBER-313 (NCT04551066) is listed as a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study of parsaclisib plus ruxolitinib compared with placebo plus ruxolitinib in participants with myelofibrosis. Listed enrollment is 252. The study began on 2021-05-24, has a primary completion date of 2023-08-03, and is marked terminated.

The primary endpoint is the percentage achieving at least a 35% reduction in spleen volume from baseline to Week 24 by MRI or applicable CT. The posted percentages are 52.8% and 46.7%. The sponsor-reported odds ratio is 1.27, with a 95% confidence interval from 0.71 to 2.26; the interval includes the no-difference value. The reason for termination, original sample-size justification, missing-data methods, and multiplicity strategy are not reported in the registry record.