COntrolled MyeloFibrosis Study With ORal JAK Inhibitor Treatment: The COMFORT-I Trial: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for COntrolled MyeloFibrosis Study With ORal JAK Inhibitor Treatment: The COMFORT-I Trial (NCT00952289), a randomized phase 3 study. The primary outcome is Number of Participants Achieving ≥ 35% Reduction in Spleen Volume From Baseline to Week 24.

2. Clinical Question

3. Trial Design

COMFORT-I was a Phase 3, randomized, double-blind, parallel-group study comparing ruxolitinib with matching placebo. The registry record lists enrollment of 309. The study began in 2009-08, had primary completion in 2010-11, and is recorded as completed. The sponsor was Incyte Corporation.

The study included participants with primary myelofibrosis, post-polycythemia vera myelofibrosis, or post-essential thrombocythemia myelofibrosis. The official title describes an oral JAK inhibitor study, while the registry intervention names are ruxolitinib and placebo. Randomization assigned treatment groups, and double masking was recorded. The parallel design means groups were assigned to their respective study interventions rather than following a crossover design as the initial allocation. The registry arm description nevertheless notes that some placebo participants could become eligible to cross over to ruxolitinib.

The primary outcome was assessed at baseline and Week 24. Its analysis population was described as all randomized participants assigned according to their original treatment group, with one exception: a participant without a baseline spleen-volume value was not included in that endpoint analysis. A separate safety population had different denominators by group, as recorded for adverse events. The registry record does not report the trial's original sample-size justification, detailed randomization procedures, or a complete statistical analysis plan. Those details should not be inferred from the posted outcome numbers.

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.

All Participants

Reasons for not completing this period:

Patients Who Crossed Over to Ruxolitinib

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population included all subjects randomized in the study. Treatment groups for this population were defined according to the treatment assignment at randomization. One patient was not included in the analysis due to a missing baseline spleen volume value.

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 Number of Participants Achieving ≥ 35% Reduction in Spleen Volume From Baseline to Week 24, measured over Baseline and Week 24.

The primary endpoint counted participants who achieved at least a 35% reduction in spleen volume from baseline to Week 24. Spleen volume was evaluated using magnetic resonance imaging, or computed tomography when magnetic resonance imaging was not suitable. A blinded central laboratory reader assessed the imaging, which limits the possibility that knowledge of assigned treatment influenced the measurement.

This is a binary endpoint: each participant is classified as meeting the response threshold or not meeting it. The reported group values therefore represent counts of participants with the event, rather than average changes in spleen volume. For the primary analysis, withdrawal, crossover to ruxolitinib before the Week 24 visit, or a missing value at that visit was treated as nonresponse. This rule makes the endpoint definition explicit for those cases, although it does not remove all possible consequences of missing data or crossover.

A threshold-based endpoint can make a result easier to interpret as a response proportion, but it does not describe the full distribution of spleen-volume change. Participants just short of the threshold and participants with no reduction are both outside the response count, despite potentially different underlying measurements. The registry record also lists maintenance of spleen response and symptom outcomes among secondary outcomes; those address different aspects of the study and should not be treated as interchangeable with the primary endpoint.

7. Results Posted in the Registry

• Ruxolitinib: 41.9% (65/155) versus 0.7% (1/153) on control; risk difference 41.3 percentage points (95% CI 33.4 to 49.2), risk ratio 64.16 (9.02–456.56); unadjusted two-proportion z-test p = <0.001.

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.

Number of Participants With a ≥ 50% Reduction in Total Symptom Score From Baseline to Week 24

• 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:
  • Ruxolitinib: 45.9% (68/148) versus 5.3% (8/152) on control; risk difference 40.7 percentage points (95% CI 31.9 to 49.5), risk ratio 8.73 (4.35–17.52); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ruxolitinib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span spleen-response maintenance, symptom response and change, and survival. The available detailed secondary result for symptom response has more participants meeting the threshold in the ruxolitinib group than in the placebo group, consistent in direction with the primary spleen-response contrast. It is a different measure, with its own scoring window and analysis population, so it adds context rather than duplicating the primary endpoint.

The registry record lists additional secondary outcomes, but detailed estimates and analyses for each are not included in the information summarized in the posted results. It is therefore not possible to describe a complete pattern across all secondary endpoints or to infer the direction of unreported outcomes. The symptom finding should not be used as a proxy for the survival outcomes or the duration of response.

Secondary findings generally carry less weight than the primary result when many outcomes are assessed, especially if the analysis plan does not describe how multiplicity was addressed. Repeated testing can make apparently strong findings more likely by chance across a family of outcomes. The registry record does not report multiplicity adjustment or a prespecified hierarchy for these secondary tests. Their interpretation should therefore remain exploratory unless the full trial analysis documents a stronger inferential framework.

The secondary data are useful for considering whether the primary result aligns with another measured domain, but they do not independently establish a comprehensive benefit profile. Differences in outcome definitions, available participants, missing observations, follow-up, and statistical procedures can affect comparability. Those details are not fully reported for all secondary endpoints in the registry record.

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

• Maintenance of a ≥ 35% Reduction From Baseline in Spleen Volume Among Patients Initially Randomized to Receive Ruxolitinib
• Duration of Maintenance of a ≥ 35% Reduction From Baseline in Spleen Volume Among Patients Initially Randomized to Receive Ruxolitinib
• Number of Participants With a ≥ 50% Reduction in Total Symptom Score From Baseline to Week 24
• Change From Baseline to Week 24 in Total Symptom Score
• Overall Survival
• Overall Survival Time
• Overall Survival - Extended Data
• Overall Survival Time - Extended Data

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary because it records whether a participant crossed a prespecified response threshold. For each group, the registry reports a count of participants with the event and a group denominator. A comparison of these proportions can be expressed as a risk difference: the event proportion in one group minus the event proportion in the other. The posted unadjusted risk difference is 0.413. The risk-difference scale is additive and directly describes the difference in event proportions, though the registry record does not provide an adjusted version of this estimate.

What does an unadjusted comparison mean?

An unadjusted comparison uses the observed group counts without accounting for other participant characteristics or prognostic factors. It describes the contrast between the randomized groups as recorded for this outcome. Randomization supports comparison of assigned groups, but it does not mean that every estimate is adjusted for baseline factors. The registry record reports a Fisher Exact test for the sponsor's analysis and the posted count-based recalculation includes an unadjusted p-value. The detailed model specification and covariate adjustments, if any, are not reported in the registry record.

Fisher's exact test evaluates the association between group assignment and a binary outcome using the observed table of counts. It is often used for categorical data, particularly when event counts are sparse. The placebo group had one recorded primary response, so a method designed for binary counts is pertinent to the reported comparison. A p-value describes how unusual data at least this discrepant would be under a null model of no group association, given the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of the difference.

Why report an interval as well as a p-value?

A p-value addresses compatibility with a null hypothesis, whereas an interval gives a range of estimates compatible with the data under the interval method. The primary risk-difference interval runs from 0.334 to 0.491. Its width reflects uncertainty in the estimated group contrast. An interval does not guarantee that the true effect lies within its endpoints, and its interpretation depends on the statistical procedure and assumptions. The registry record's posted comparison gives the interval values, but the method used to construct that recalculated interval is not described in the record.

Risk ratios and odds ratios are alternative ways to describe binary outcomes. A risk ratio compares the event proportions as a ratio; an odds ratio compares event odds. These measures answer a related but different question from the risk difference, and their numerical scale is not directly interchangeable with the additive risk-difference scale. Because the placebo response count is very small, ratio measures can be especially sensitive to the sparse reference count. They should be interpreted together with the group counts and interval estimates rather than in isolation.

What does over-dispersion mean for other outcome types?

General statistical explanation: over-dispersion occurs when observed variability is greater than a model assumes. It can make standard errors too small and intervals too narrow if the model does not account for the extra variation. The primary outcome is a binary count, and the posted analysis is a Fisher Exact comparison rather than a count-rate model. The registry record does not report an over-dispersion adjustment for this endpoint. This general issue should not be mistaken for a reported feature of the COMFORT-I primary analysis.

For the symptom secondary endpoint, the registry reports a count of participants reaching a reduction threshold. Its recalculated risk difference is 0.407, with an interval from 0.319 to 0.495, and an unadjusted p-value of p < 0.001. These statistics use that outcome's own group counts; they do not estimate the primary spleen endpoint. The secondary outcome has its own definition of baseline and Week 24 symptom scores, based on averages of daily scores over the stated periods. A threshold outcome similarly simplifies a continuous score change into responder and nonresponder categories.

Interpretation of any significance test also depends on whether the test was planned and how many outcomes or comparisons were considered. If many hypotheses are tested, the chance of at least one small p-value can increase unless the analysis accounts for multiplicity. General statistical practice may address this through prespecified testing sequences or adjusted error rates, but the registry record does not report such a procedure for the posted secondary outcomes. The secondary results therefore warrant more caution than a single prespecified primary comparison, particularly when their multiplicity handling is not documented.

The registry's endpoint population definition is relevant to the methods. The primary endpoint was described as intent-to-treat according to randomized assignment, while the record states that one participant without a baseline spleen-volume value was not included in the analysis. For the Week 24 response, withdrawal, crossover before the visit, or a missing visit value was classified as nonresponse. These choices define the analysis dataset and event classification; they should be considered when interpreting the estimate. Further sensitivity analyses, imputation methods, or reasons for missing observations are not reported in the registry record.

Finally, the posted recalculations are simple unadjusted re-calculations from the reported summary counts. They are useful for describing the event proportions and a direct group contrast, but do not replace the sponsor's full analysis. The sponsor's reported Fisher Exact result remains the trial's own analysis. The registry record does not provide enough detail to reconstruct every element of that analysis, including its full protocol-level statistical plan.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.413, with an interval from 0.334 to 0.491. The interval gives a sense of the precision of the estimated group contrast: values closer together indicate greater statistical precision, while a wider range reflects more uncertainty. The interval is not a guarantee about the true effect, and its interpretation depends on the method and assumptions used to construct it.

The reported group counts are 65 of 155 participants for ruxolitinib and 1 of 153 for placebo. The contrast is therefore strongly shaped by the very small number of placebo participants meeting the response threshold. Such sparse events can make relative measures, including risk ratios and odds ratios, less stable; their reported intervals are correspondingly broad. The risk difference is often more directly interpretable as an absolute contrast, but it too has uncertainty, reflected in its interval.

The reported sponsor test gives p < 0.001, while the unadjusted recalculation gives p < 0.001. These are compatible statements at different levels of precision, not contradictory findings. A p-value alone does not convey the range of plausible effect sizes. The interval and the observed counts help show both the direction and precision of the estimated contrast.

Precision is distinct from clinical importance and generalizability. A relatively precise estimate for this endpoint does not establish the outcome's importance to every participant, nor does it show how the result applies beyond the trial population or at other time points. The registry record does not report additional interval estimates for every secondary outcome or a full account of uncertainty across all outcomes.

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 calculations. They are expressed as participants per arm for the binary outcomes in this trial, rather than as a total number of events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect being planned for is the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect and the statistical model were correct. The 90% power column gives the corresponding planning figure for a higher target chance of detection. These are design calculations, not guarantees that a future study will reach its target or produce a particular result.

Rows planning for 100%, 75%, and 50% of the observed effect consider progressively smaller effects. Smaller effects generally require more participants to distinguish them from random variation at a fixed significance level and target power. For example, the planning rows show that the participant requirements increase as the assumed fraction of the observed effect decreases. The values are illustrations based on this trial's observed contrast, not independently justified estimates of the effect a future study should expect.

This is not observed power. The registry record does not report the original sample-size justification or the assumptions used when COMFORT-I was planned. The planning calculations should therefore be read only as hypothetical illustrations under their stated assumptions, not as a reconstruction of the trial's own design process.

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 = 0.007; treatment proportion p₁ = 0.419; average p̄ = 0.213.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5790 = 1.1347.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5000 = 0.4208.
4. n = (1.1347 + 0.4208)² / (0.4128)² = 14.2, rounded up to 15 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 <- 0.0065359477124183                          # control proportion
p1 <- 0.419354838709677                          # 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(952289)
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 = 15 (80% power), 19 (90% power)
 75% of observed effect: n per arm = 21 (80% power), 28 (90% power)
 50% of observed effect: n per arm = 35 (80% power), 47 (90% power)
power.prop.test: 14.2 
Simulated power at n = 15 per arm: 0.905 (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 sponsor's reported primary analysis used Fisher Exact and reported p < 0.001 for the comparison. The unadjusted recalculation from the posted group counts reports p < 0.001 and a risk difference of 0.413, with an interval from 0.334 to 0.491. Both p-value statements indicate strong evidence against the null of no group association under their respective analyses; their difference in displayed precision does not mean they conflict.

The recalculated estimate is a simple description of the group counts, not a replacement for the trial's own analysis. The registry record does not provide the sponsor's full statistical plan or enough detail to reproduce every aspect of the reported test. The sponsor's own analysis takes precedence as the trial analysis. No discrepancy between the posted summary and the recalculation is flagged in the registry information.

The p-value should not be interpreted as an effect-size estimate. The risk difference and its interval describe magnitude and uncertainty on an absolute scale, while Fisher Exact supplies the reported test result. Together they provide distinct information. Neither resolves questions about missing data, the handling of multiple outcomes, or applicability beyond the studied population.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators evaluate more than one endpoint, comparison, time point, or subgroup. The more hypotheses considered, the greater the opportunity for a nominally small p-value to occur by chance somewhere in the set. A prespecified testing hierarchy or an adjustment to the testing procedure can control the overall error rate, but the registry record does not report whether such a strategy was used for the secondary outcomes. The results for those endpoints should therefore be interpreted cautiously rather than as a collection of equally confirmatory findings.

The primary endpoint analysis was described as intent-to-treat, with treatment groups defined by randomized assignment. The record also states that one participant was not included in the analysis because baseline spleen volume was missing. This means the posted primary endpoint analysis did not include every randomized participant as described in the population definition. The record does not report a sensitivity analysis addressing this exclusion or the reason the baseline value was unavailable.

At Week 24, the endpoint definition classified participants who withdrew, crossed over to ruxolitinib before the visit, or had a missing value as nonresponders. This is an explicit outcome rule, not a statistical imputation of the unobserved measurement. It can affect the estimated response count if missingness or crossover differs between groups. The registry record does not report the numbers or reasons for those situations, nor does it describe alternative missing-data analyses.

The arm description notes an opportunity for some placebo participants to cross over, while the primary endpoint definition specifies how a pre-visit crossover was treated. Further crossover criteria and their impact on other outcomes are not reported in the registry record. Details of interim analyses, stopping rules, and the original statistical plan are also not reported in the registry record, so no assumptions about them should be made.

16. Safety Results

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

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 (6.5%), abdominal pain (4.0%), anaemia (3.2%), splenic infarction (2.6%), fatigue (2.6%).

The posted safety figures report serious adverse events affecting 43 of 155 participants in the ruxolitinib group and 53 of 151 in the placebo group. Other adverse events affected 150 of 155 and 147 of 151, respectively. These are counts within the safety populations recorded for each group; their denominators differ from the primary endpoint analysis denominators. They should not be combined with the efficacy counts or treated as a direct estimate of causal risk without the trial's detailed safety analysis.

The listed serious adverse-event terms include pneumonia at 6.5%, abdominal pain at 4.0%, anaemia at 3.2%, splenic infarction at 2.6%, fatigue at 2.6%, and cardiac failure congestive at 2.0%. These entries describe reported serious-event terms, not a complete account of all possible harms or their severity and timing. The registry record does not report death counts in the posted safety fields. These figures alone do not establish whether an event was caused by study treatment or whether differences between groups are statistically reliable.

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

The primary result describes a clear difference in the recorded Week 24 spleen-volume response counts between the randomized groups. The risk-difference estimate and its interval quantify the contrast and its statistical uncertainty, while the sponsor's Fisher Exact test reports a small p-value. The secondary symptom response points in the same direction in the available detailed results, but it remains a separate outcome.

The result does not establish that every participant receiving ruxolitinib experienced a response, or that a participant not meeting the threshold had no change. A threshold-based count compresses a range of possible measurements into responder and nonresponder categories. It also does not, by itself, describe durability of response, survival, or the full course of symptoms. Those questions require separate outcomes and their detailed results.

The figures do not settle the interpretation of safety. Serious and other adverse-event counts are recorded for safety populations, but event attribution, severity, timing, and uncertainty need fuller analysis. They also do not resolve the effect of missing values or crossover on the endpoint, despite the specified nonresponder rule.

General statistical context: a randomized comparison can support an estimate of a group contrast, but interpretation also depends on how participants were analyzed, outcome definitions, missing data, multiplicity, and the extent to which the studied population resembles the population of interest. The registry record contains some of these details but not a full statistical plan or all secondary results. The findings should therefore be read as evidence about the defined endpoint and study population, not as a complete account of all outcomes or all possible settings.

No treatment recommendation follows from these statistics alone. Clinical meaning depends on the importance of the endpoint, the broader evidence, and individual context, which are not determined by the response counts or p-value in isolation.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can be summarized using a clinically defined binary endpoint and a direct contrast between groups. The primary measure is understandable as the number meeting a specified imaging response threshold, and the blinded central reading helps limit observer influence on the imaging assessment. The risk difference complements the raw counts by expressing the absolute group contrast, while its interval conveys uncertainty.

The result also shows why p-values and effect estimates should be read together. The sponsor's Fisher Exact test gives a significance result, but the risk difference and its interval are more informative about the size and precision of the observed contrast. Sparse events in the placebo group also make it important to distinguish absolute and relative measures rather than relying on a ratio alone.

Several statistical issues remain relevant despite a strong primary contrast. The endpoint uses a threshold, the missing-data rule treats specified cases as nonresponse, and the primary analysis excluded a participant with missing baseline spleen volume. The registry lists multiple secondary outcomes, while its record does not state how multiplicity was handled. These features illustrate why an impressive primary result does not remove the need to examine analysis populations, outcome definitions, and the breadth of testing.

Finally, the planning illustrations based on the observed effect should not be confused with the original design assumptions. The registry record does not report the original sample-size justification. Keeping trial design information distinct from retrospective planning calculations is essential when interpreting power, precision, and what a future study might require.

19. Limitations

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

The primary endpoint is a threshold response at Week 24. It does not describe the complete distribution of spleen-volume changes, and participants just below the threshold are grouped with those showing little or no change. The registry record does not provide a continuous summary of primary spleen-volume change in the posted primary result.

The endpoint analysis population is described as intent-to-treat, but one participant with a missing baseline spleen-volume value was not included. For missing Week 24 values, withdrawals, and pre-visit crossovers, the analysis classified participants as nonresponders. This rule is explicit, but the registry record does not report the counts, reasons, group distribution, or sensitivity analyses needed to assess the impact of these situations.

The available safety populations have denominators different from the primary endpoint groups. The registry record gives adverse-event counts and selected serious-event terms, but not the detail needed to compare event timing, severity, treatment attribution, or uncertainty. Death counts are not reported in the registry record.

Although secondary outcomes include symptom measures, response maintenance, and survival, the full set of detailed results is not available in the registry information described. The record also does not report how multiplicity was controlled, the full analysis plan, interim analyses, or the original sample-size assumptions. It is therefore not possible to determine from this record alone how all secondary hypotheses were prioritized or how the trial's planned statistical procedures compare with the simple recalculations.

The conclusions from the primary analysis are tied to the specified population, outcome definition, and time point. Broader interpretation requires information beyond the posted primary counts and should not be inferred from the unadjusted comparison alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: COntrolled MyeloFibrosis Study With ORal JAK Inhibitor Treatment: The COMFORT-I Trial — NCT00952289.
• Registry record last updated 2018-03-12; status last verified 2018-02.
• Results first posted 2012-01-24.
• 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

COMFORT-I was a completed Phase 3 randomized, double-blind, parallel-group trial of oral ruxolitinib versus matching placebo in participants with primary myelofibrosis, post-polycythemia vera myelofibrosis, or post-essential thrombocythemia myelofibrosis. The primary endpoint counted participants achieving at least a 35% spleen-volume reduction from baseline to Week 24.

The posted primary counts were 65 of 155 participants for ruxolitinib and 1 of 153 for placebo. The unadjusted risk difference was 0.413, with an interval from 0.334 to 0.491; the sponsor's reported Fisher Exact result was p < 0.001. The record also includes a secondary symptom-response result and safety counts. Interpretation is limited by the endpoint's threshold definition, specified nonresponder handling, an excluded baseline-missing participant, incomplete secondary reporting, and the absence of a reported multiplicity plan.