Phase III Study of SAR302503 in Intermediate-2 and High Risk Patients With Myelofibrosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase III Study of SAR302503 in Intermediate-2 and High Risk Patients With Myelofibrosis (NCT01437787), a randomized phase 3 study. The primary outcome is Response Rate (RR): Percentage of Participants Who Had a >=35% Reduction From Baseline in Volume of Spleen Size at The End Cycle 6.

2. Clinical Question

The objective also included evaluating myelofibrosis-associated symptoms, overall survival, progression-free survival, durability of splenic response, and safety. The posted efficacy results focus on the Cycle 6 spleen-volume response and two secondary response outcomes. The registry record identifies the trial as a crossover study, but does not report enough detail to describe the crossover sequence or how crossover data were handled in the primary efficacy analysis.

3. Trial Design

This was a Phase 3, multicenter, randomized, double-blind, placebo-controlled study with three arms: placebo, SAR302503 400 mg, and SAR302503 500 mg. The registry record lists the model as crossover. The record gives an enrollment of 289 and a status of terminated. It lists a start date of 2011-12-31 and a primary completion date of 2014-06-30. The reason for termination is not reported in the registry record.

The study population included people with Intermediate-2 or high-risk primary myelofibrosis, post-polycythemia vera myelofibrosis, or post-essential thrombocythemia myelofibrosis with splenomegaly. The primary outcome description defines the intention-to-treat population as all randomized participants who signed an informed consent form. The registry record describes imaging at baseline and the end of Cycle 6, with a confirmatory scan approximately 4 weeks later. MRI was specified, with CT for participants with contraindications for MRI; an Independent Review Committee reviewed imaging results in a blinded manner.

The arm descriptions specify once-daily oral administration for 28 days, on an empty stomach at approximately the same time each day. The registry record does not explain how this dosing description relates to the crossover model, the treatment periods, or the transition between trial phases. Those details are not reported in the registry record.

Enrollment counts in the posted primary outcome are 96 for placebo, 96 for SAR302503 400 mg, and 97 for SAR302503 500 mg. The available results describe the primary outcome and two secondary outcomes, but the registry record reports no analyses in its analyses listing. It does not report the original sample-size justification, the planned statistical analysis methods, or details of any interim analyses.

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: Of 351 screened participants, 62 were screen failures and 289 were randomized.

Randomization until end of Cycle 6

Reasons for not completing this period:

Crossover After Cycle 6

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

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Response Rate (RR): Percentage of Participants Who Had a >=35% Reduction From Baseline in Volume of Spleen Size at The End Cycle 6, measured over Baseline, Week 24.

The primary endpoint is a binary response: whether a participant had at least a 35% reduction from baseline in spleen volume at the end of Cycle 6. The reported outcome is the percentage of participants meeting that threshold, with a 95% confidence interval. Spleen volume was measured by MRI, or CT when MRI was contraindicated. The description specifies a confirmatory scan approximately 4 weeks after the end of Cycle 6, and says imaging was reviewed in a blinded manner by an Independent Review Committee.

A threshold-based response endpoint translates a continuous measurement, spleen volume, into an indicator of whether each participant reached a prespecified level of change. As a general statistical point, this can make a result easier to interpret as a proportion of participants meeting a criterion, while discarding information about the size of changes that fall short of or exceed that criterion. The registry record reports the percentage meeting the threshold, not the full distribution of individual spleen-volume changes.

The endpoint is used to assess the trial’s primary efficacy objective: reduction in spleen volume. It does not by itself describe symptom burden, survival, durability, or safety. Those were separate objectives or outcomes. The posted results describe the primary analysis population as all randomized participants who signed an informed consent form. The registry record does not provide details about how missing imaging, absent confirmatory scans, or other incomplete outcome data were handled.

7. Results Posted in the Registry

• SAR302503 400 mg: 36.5% (35/96) versus 1.0% (1/96) on control; risk difference 35.4 percentage points (95% CI 25.6 to 45.3), risk ratio 35.00 (4.89–250.36); unadjusted two-proportion z-test p = <0.001.
• SAR302503 500 mg: 40.2% (39/97) versus 1.0% (1/96) on control; risk difference 39.2 percentage points (95% CI 29.2 to 49.1), risk ratio 38.60 (5.41–275.33); 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.

Symptom Response Rate (SRR): Percentage of Participants With >=50% Reduction From Baseline in the Total Symptom Score at End of Cycle 6

• 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:
  • SAR302503 400 mg: 36.3% (33/91) versus 7.1% (6/85) on control; risk difference 29.2 percentage points (95% CI 17.9 to 40.5), risk ratio 5.14 (2.27–11.64); unadjusted two-proportion z-test p = <0.001.
  • SAR302503 500 mg: 34.1% (31/91) versus 7.1% (6/85) on control; risk difference 27.0 percentage points (95% CI 15.9 to 38.2), risk ratio 4.83 (2.12–10.99); 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 SAR302503 400 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for SAR302503 500 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Had >=25% Reduction From Baseline in Volume of Spleen Size at End of Cycle 6

• 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:
  • SAR302503 400 mg: 49.0% (47/96) versus 2.1% (2/96) on control; risk difference 46.9 percentage points (95% CI 36.5 to 57.3), risk ratio 23.50 (5.87–94.02); unadjusted two-proportion z-test p = <0.001.
  • SAR302503 500 mg: 51.5% (50/97) versus 2.1% (2/96) on control; risk difference 49.5 percentage points (95% CI 39.1 to 59.8), risk ratio 24.74 (6.19–98.83); 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 SAR302503 400 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for SAR302503 500 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The two posted secondary outcomes show a broadly consistent direction across comparisons: the observed response percentages are higher in both SAR302503 arms than in placebo. One outcome concerns symptom response, defined using a reduction in total symptom score; the other uses a lower threshold for reduction in spleen volume than the primary endpoint. These outcomes provide related but distinct information: one concerns symptoms, while the other remains an imaging-based spleen response.

This pattern is directionally consistent with the primary result, which also reports higher response percentages in the active arms than in placebo. The secondary outcomes therefore add context to the primary endpoint, but they do not substitute for it. Symptom assessment and imaging response measure different aspects of the disease, and the definitions and analysis populations differ across outcomes. In particular, the posted symptom outcome has different arm denominators from the primary analysis.

The reported secondary comparisons have unadjusted p-values of <0.001. Those results should carry less inferential weight than a prespecified primary analysis when multiple outcomes and comparisons are considered. As a general statistical point, testing multiple hypotheses increases the chance of obtaining at least one apparently unusual result by chance unless the analysis plan accounts for multiplicity. The registry record does not report whether a hierarchy, family-wise error adjustment, or other multiplicity procedure was planned or used.

The registry record lists no reported analyses for the secondary outcomes. Thus, the posted results permit description of their observed pattern and unadjusted comparisons, but do not reveal whether or how the trial investigators interpreted them under a prespecified statistical plan. Neither secondary endpoint establishes a result for survival or durability, which were objectives but are not reported among these posted outcome results. The direction of the secondary findings is supportive context, not an independent confirmation that resolves the limitations of the primary comparison.

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

• Symptom Response Rate (SRR): Percentage of Participants With >=50% Reduction From Baseline in the Total Symptom Score at End of Cycle 6
• Percentage of Participants Who Had >=25% Reduction From Baseline in Volume of Spleen Size at End of Cycle 6

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant either met the threshold of at least a 35% reduction in spleen volume or did not. The posted arm results express the number meeting that criterion as a percentage, alongside a 95% confidence interval. The registry record defines the primary analysis population as all randomized participants who signed an informed consent form. It does not provide a fuller statistical analysis plan.

What does a response percentage describe?

A response percentage describes the share of participants in an arm who met the endpoint definition. It is distinct from the average change in spleen volume. A threshold endpoint can be useful when the clinical question is framed around reaching a specified degree of reduction, but it does not show how far each participant’s result was from the threshold. As a general statistical point, categorizing a continuous measurement can simplify interpretation while losing detail about variation in the underlying measurements.

The posted results give arm-specific response percentages and confidence intervals. The comparison results express the contrast between each SAR302503 arm and placebo as a risk difference. In general, a risk difference is the difference between the two response proportions on the probability scale. Positive values in this setting correspond to a higher observed response proportion in the named SAR302503 arm than in placebo. The reported estimates are 0.354 for 400 mg versus placebo and 0.392 for 500 mg versus placebo. Their confidence intervals are 0.256 to 0.453 and 0.292 to 0.491, respectively.

How should the p-values be understood?

The posted unadjusted p-values for both primary comparisons are <0.001. A p-value describes how compatible the observed data are with a specified null hypothesis under the statistical test and its assumptions; it is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The registry record does not identify the test used for these p-values, provide a multiplicity adjustment, or list a sponsor-reported analysis for these comparisons. They should therefore be read as unadjusted results as labeled, not as evidence that all design and analysis uncertainties have been resolved.

The comparisons are reported separately for each dose against placebo. A direct contrast between the two active doses is not reported. It would not be appropriate to infer a dose difference solely from the separate placebo comparisons, because those comparisons do not directly test the difference between active arms.

Why does the confidence interval matter?

A confidence interval gives a range of values compatible with the data under the method used to calculate it. In general, a narrower interval indicates greater precision and a wider interval indicates more uncertainty. The interval is not a guarantee that the true value lies within its endpoints, and it does not capture every potential source of bias, such as missing data or limitations in the design. The primary arm intervals and comparison intervals describe different quantities: the former concern each group’s response percentage, while the latter concern the difference between a treatment arm and placebo.

Imaging was assessed at baseline and at the end of Cycle 6, with a confirmatory scan approximately 4 weeks later. The registry record says an Independent Review Committee reviewed imaging in a blinded manner. This describes an important feature of outcome assessment, but the record does not state how a participant’s response was classified when an assessment or confirmatory scan was unavailable. It also does not describe imputation, sensitivity analyses, or other missing-data procedures.

The record identifies a crossover model, but does not give the treatment sequence, timing of crossover, or whether the primary outcome analysis used only a particular period. As a general statistical point, crossover can affect how observations are interpreted because participant outcomes may relate to more than one treatment period. Without the protocol and analysis details, the posted primary comparison cannot be reconstructed in relation to that design feature.

The results include a planned sample-size illustration based on observed effects. Such calculations describe planning scenarios under specified assumptions; they do not establish the trial’s original sample-size rationale. The original design assumptions, including the trial’s own anticipated treatment effect and target enrollment justification, are not reported in the registry record. In general, power is the probability of detecting a specified effect under a stated model when that effect is present; it is not a property that can be inferred from the observed result alone.

For binary outcomes, the precision of an estimate depends in part on the number of participants and the distribution of responses. General statistical principle: when response events are uncommon, estimates can be especially sensitive to a small number of observations, and intervals may be less stable. That context is relevant to reading low response proportions, but it does not replace the reported confidence intervals. No additional model-based adjustment should be inferred from the posted percentages or comparisons.

11. Confidence Intervals and Precision

The primary response percentages have 95% confidence intervals of 0.0% to 3.1% for placebo, 26.8% to 46.1% for SAR302503 400 mg, and 30.4% to 50.0% for SAR302503 500 mg. The intervals convey uncertainty around each arm’s response proportion, rather than the uncertainty around a direct comparison. The comparison intervals are reported separately: 0.256 to 0.453 for the 400 mg versus placebo risk difference, and 0.292 to 0.491 for the 500 mg versus placebo risk difference.

As a general statistical explanation, a confidence interval describes a range of values reasonably compatible with the data under the method used. It is not a prediction interval for individual participants, and it does not address every source of uncertainty. For example, interval width does not quantify possible effects of missing outcome data, departures from the analysis assumptions, or limitations in how the trial design is documented.

The arm-level intervals show that the point estimates are not known with perfect precision. The placebo interval includes values from 0.0% to 3.1%; the active-arm intervals also cover ranges around their respective point estimates. The risk-difference intervals provide a more direct comparison with placebo, and both reported intervals are above zero. This describes the posted unadjusted comparisons; it does not establish the results of any unreported adjusted or sponsor analysis.

Precision should also be considered alongside the trial’s population and endpoint definition. These estimates concern participants in the registry-defined analysis population and a threshold response assessed at the end of Cycle 6 with confirmation approximately 4 weeks later. They do not describe the precision of survival, long-term response durability, or outcomes for groups not represented by the eligibility description. The registry record does not report sensitivity analyses that might show how the intervals or estimates change under alternative assumptions.

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 entries are planning illustrations, not observed trial results. For these binary outcomes, the displayed figures are participants per arm, rather than total events. The stated planning 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 a stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned participants per arm under the specified assumptions for a calculation targeting 80% power to detect the stated effect. The 90% power column gives the corresponding participants per arm for a calculation targeting 90% power. In general, power describes the chance that a study would detect an effect of the specified size under the assumed model if that effect were present. Higher target power generally requires more participants under otherwise similar assumptions.

Rows describing 100%, 75%, and 50% of the observed effect use progressively smaller target effects. A smaller effect is harder to distinguish from random variation, so it requires more participants per arm under the planning assumptions. Each entry applies to the comparison and endpoint represented by its row; it is not a universal target for a future study. The values are not a reconstruction of the trial’s original design and do not establish how the trial was planned. This is not observed power.

The plotted curve is another way to read the relationship between assumed sample size and the planning calculation: it illustrates how the calculated power changes under the stated assumptions. Its interpretation remains conditional on the effect size and calculation method. Because the registry record does not report its original design assumptions, these illustrations should not be treated as evidence of the trial’s prespecified power or of the adequacy of its original enrollment target.

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 = 0.010; treatment proportion p₁ = 0.365; average p̄ = 0.188.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5520 = 1.0819.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4919 = 0.4140.
4. n = (1.0819 + 0.4140)² / (0.3542)² = 17.8, rounded up to 18 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 <- 0.0104166666666667                          # control proportion
p1 <- 0.364583333333333                          # 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(1437787)
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 = 18 (80% power), 24 (90% power)
 75% of observed effect: n per arm = 27 (80% power), 35 (90% power)
 50% of observed effect: n per arm = 44 (80% power), 58 (90% power)
power.prop.test: 17.8 
Simulated power at n = 18 per arm: 0.890 (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

The trial has a primary endpoint, two posted secondary outcomes, and several objectives described in the registry summary. The posted comparison results include unadjusted p-values. The registry record does not report a multiplicity strategy, such as a prespecified testing sequence or an adjustment to account for testing more than one endpoint or comparison. Without that information, the p-values should not be interpreted as if they necessarily control the overall false-positive rate across the full set of outcomes.

The record describes an intention-to-treat population for the primary endpoint as all randomized participants who signed an informed consent form. That definition helps identify the intended analysis population. However, the registry record does not describe how missing imaging measurements, absent confirmatory scans, or participants without an evaluable response were handled. It does not report imputation methods, sensitivity analyses, or a detailed participant flow for each endpoint. Consequently, the posted response percentages alone do not show whether missing outcome data could have affected the estimates.

The primary endpoint is described as based on imaging at baseline and the end of Cycle 6, with confirmation approximately 4 weeks later. An Independent Review Committee reviewed imaging results in a blinded manner. The record does not state the exact rules for classifying a response when the initial and confirmatory assessments differed, or how the analysis treated missing or non-evaluable scans. These procedures are not reported in the registry record.

The trial is identified as crossover, but the registry record does not provide the sequence, timing, or analysis approach for crossover. It is therefore not possible from this record to determine how treatment periods contributed to each outcome or how possible period effects were addressed. The record also reports no analyses listing, no original sample-size justification, and no detailed statistical plan. These omissions do not alter the arithmetic of the posted results, but they limit independent assessment of whether the analysis followed a prespecified approach.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaemia (8.6%), vomiting (5.6%), wernicke's encephalopathy (5.6%), cardiac failure (5.2%), pneumonia (4.2%).

The safety results list serious adverse events and other adverse events separately, with affected counts and the number at risk for each group. In the initial groups, serious adverse events were reported for 22 of 95 participants in placebo, 37 of 96 in SAR302503 400 mg, and 43 of 97 in SAR302503 500 mg. Other adverse events were reported for 76 of 95, 96 of 96, and 94 of 97, respectively. Death counts listed for these groups are 6, 5, and 6. The registry record also gives separate counts for the SAR302503 groups after crossover; those should be read as separate reported groups, not combined with the initial groups.

The serious adverse event terms listed most often include anaemia at 8.6%, vomiting at 5.6%, Wernicke's Encephalopathy at 5.6%, cardiac failure at 5.2%, pneumonia at 4.2%, and ascites at 3.2%. These are registry-reported safety figures, not evidence that an event was caused by a particular treatment. The record does not provide a statistical comparison of safety outcomes, exposure-adjusted rates, or detailed event timing. The counts alone also do not describe severity beyond the registry’s serious-event classification.

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

The posted results describe the percentage of participants who met a defined imaging response threshold at a specified assessment time. They show higher observed primary response percentages in the SAR302503 groups than in placebo, with reported unadjusted risk-difference comparisons and confidence intervals. This is evidence about that endpoint in the registry-defined analysis population; it is not a complete summary of the treatment’s effects across all outcomes.

The response measure does not show how much spleen volume changed for every participant, nor does it describe symptom burden, survival, progression-free survival, or the durability of response. Those outcomes were objectives or secondary outcomes, but the registry record does not provide posted results for survival, progression-free survival, or durability in the material. The secondary symptom and spleen-volume results offer additional outcome-specific information, but their unadjusted status and the absence of reported multiplicity methods limit how strongly they can be interpreted as confirmatory.

A trial result is not a guarantee of an individual outcome. The arm-level percentages describe the observed groups, and the confidence intervals convey statistical uncertainty under the methods used. They do not capture every possible source of uncertainty, including missing data, design features not documented in the registry, or differences between the enrolled population and other populations.

The registry record identifies the study as terminated but does not report why. It also identifies a crossover model without explaining its implementation or analysis. As a result, the record does not support a complete evaluation of the trial’s conduct or the effect of crossover on the estimates. The results should therefore be understood as the posted outcome data and unadjusted comparisons, with those documentation limits kept in view.

Finally, a statistically small unadjusted p-value does not by itself establish clinical importance, long-term benefit, or a favorable overall balance of outcomes. The record includes safety counts, but does not present a comparative safety analysis or a combined assessment of benefits and harms. The posted statistics answer a narrower question: how often participants met the specified response definition in the recorded groups.

17. Why This Trial Matters Statistically

This trial is statistically informative because it reports a clearly defined, threshold-based imaging outcome in three randomized groups and gives both arm-level response estimates and comparison intervals. The endpoint includes a confirmatory imaging assessment, and the registry record states that imaging was reviewed in a blinded manner by an Independent Review Committee. Those features make the endpoint definition and assessment process important parts of interpreting the reported response percentages.

The record also illustrates why an effect estimate and its uncertainty should be considered together. The response percentages communicate how often the endpoint was met in each group, while the risk differences express the comparison with placebo. Confidence intervals show that these estimates are not exact values. The unadjusted p-values add a measure tied to a null-hypothesis test, but do not replace effect size, interval precision, or a documented analysis plan.

Several design and reporting issues matter statistically. The record labels the trial crossover but does not describe the sequence or the treatment-period analysis. It reports no analyses listing, no original sample-size justification, and no multiplicity plan. It also does not describe missing-data procedures. These gaps constrain independent review of the assumptions and methods behind the results, even though the outcome values themselves are available.

The two secondary outcomes show related patterns, one based on symptoms and one based on a different spleen-volume threshold. Their distinction from the primary outcome and their unadjusted comparisons matters when assessing how much corroboration they provide. This is a useful example of why outcome families, populations, and analysis plans need to be considered rather than treating each reported p-value as an isolated conclusion.

Finally, the safety record presents affected counts and serious adverse event terms alongside efficacy outcomes. A statistical reading keeps those data descriptive unless a comparative safety analysis is reported. Taken together, the trial illustrates how endpoint definition, design transparency, multiplicity, missingness, and precision shape what can be concluded from posted clinical trial results.

18. Limitations

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

Several limitations are specific to the registry record for this trial. It identifies the study as a crossover design but does not report the treatment sequence, crossover timing, period structure, or the method used to analyze outcomes after crossover. Separate post-crossover safety groups are listed, but the record does not explain their relationship to the original randomized groups or how those observations were handled in efficacy analyses.

The trial status is terminated, but the reason for termination is not reported in the registry record. The record lists an enrollment of 289, yet it does not provide the original sample-size justification or enough design assumptions to evaluate the planned enrollment target. Planning illustrations based on observed effects are not a substitute for the original design rationale.

Although the primary endpoint description specifies a population and imaging schedule, missing-data handling is not reported. The record does not explain how absent scans, missing confirmation, or non-evaluable outcomes were treated. It also does not report sensitivity analyses that could test whether conclusions depend on those choices.

The outcome set includes multiple primary and secondary comparisons, but a multiplicity strategy is not reported. The registry record does not list analyses or give a detailed statistical analysis plan. As a result, it is not possible to determine from the record whether the posted unadjusted p-values correspond to a prespecified analysis strategy or how confirmatory the secondary results were intended to be.

Finally, posted results for overall survival, progression-free survival, and durability of splenic response are not included in the outcomes described. The available data therefore provide a limited view of the stated objectives and do not permit a complete assessment of longer-term outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase III Study of SAR302503 in Intermediate-2 and High Risk Patients With Myelofibrosis — NCT01437787.
• Registry record last updated 2026-08-11; status last verified 2026-07.
• Results first posted 2026-08-11.
• 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

NCT01437787 is a randomized, double-blind, placebo-controlled Phase 3 study of SAR302503 400 mg, SAR302503 500 mg, and placebo in participants with specified forms of Intermediate-2 or high-risk myelofibrosis and splenomegaly. The registry record lists a crossover model, an enrollment of 289, and a terminated status.

The primary outcome was the percentage meeting at least a 35% spleen-volume reduction threshold at the end of Cycle 6, assessed by imaging with confirmation approximately 4 weeks later. The posted response percentages were 1.0% for placebo, 36.5% for 400 mg, and 40.2% for 500 mg; both posted unadjusted comparisons have p-values of <0.001.

The record also includes symptom response, a secondary spleen-volume threshold, and descriptive safety counts. It does not report the reason for termination, the original sample-size rationale, a multiplicity strategy, missing-data methods, or details of the crossover analysis.