Clinical Study Assessing the Efficacy and Safety of Macitentan in Fontan-palliated Subjects: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Study Assessing the Efficacy and Safety of Macitentan in Fontan-palliated Subjects (NCT03153137), a randomized phase 3 study. The primary outcome is Change From Baseline in Peak Oxygen Uptake/Consumption (VO2) Up to Week 16.

2. Clinical Question

3. Trial Design

This was a Phase 3, prospective, multicenter, randomized, double-blind, placebo-controlled, parallel-group study of macitentan in Fontan-palliated adult and adolescent participants. The study was sponsored by Actelion. The registry record lists enrollment of 142 and a completed status. The recorded start date is 2017-08-14, and the primary completion date is 2021-06-30.

Participants were assigned to macitentan 10 mg per day or placebo. Both treatments were film-coated tablets for oral use. Randomization and a parallel-group design mean that participants were allocated to one of the treatment groups, with outcomes compared between groups. The registry describes masking as quadruple. It does not report in this record summary the identities of the masked roles, the allocation ratio, or the methods used to generate and conceal the random sequence.

The primary outcome was change from baseline in peak oxygen uptake through Week 16, measured in mL/kg/min. The full analysis set included all participants randomized to study treatment. The posted primary group summaries include 69 participants in the placebo group and 68 in the macitentan group. The record also lists secondary outcomes concerning peak oxygen uptake through Week 52, physical activity through Week 16, adverse events, blood pressure, pulse rate, and oxygen saturation.

The registry lists 27 outcome measures and 26 posted secondary outcomes. The statistical analysis plan, original sample-size justification, detailed visit schedule, and protocol deviations are not reported in the registry record. Those omissions limit what can be inferred about the study’s planned analysis choices or how closely the posted analyses follow the original protocol.

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: A total of 142 participants were enrolled, out of which 137 participants were included in the analysis as 5 participants were excluded due to regulatory restrictions.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included all participants randomized to the study treatment.

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 Change From Baseline in Peak Oxygen Uptake/Consumption (VO2) Up to Week 16, measured over Baseline up to Week 16.

Peak oxygen uptake, or peak VO2, is the maximum rate at which oxygen is taken up during exercise, expressed in milliliters per kilogram per minute. The primary endpoint is the change from baseline through Week 16. It is a continuous measure: each participant’s result can take a range of values rather than being classified only as an event or no event.

Cardiopulmonary exercise testing measures exercise capacity under a standardized test setting. In general, peak oxygen uptake is used as an exercise-capacity outcome because it quantifies oxygen uptake achieved during exertion. A change-from-baseline endpoint expresses how the measure changed over the specified follow-up period, while a between-group comparison asks whether the average change differed between assigned treatments.

The registry describes the primary outcome as a mean change and reports standard deviations for the group summaries. The posted mean change was -0.67 mL/kg/min in the placebo group and -0.16 mL/kg/min in the macitentan group. These summaries describe the participants included in each group’s posted outcome data; they do not by themselves establish the result of the sponsor’s adjusted comparison.

The endpoint is specific to the recorded time point: it concerns change through Week 16. The registry separately lists a secondary peak VO2 outcome through Week 52. These are distinct follow-up outcomes and should not be treated as interchangeable. The record does not report in the information the detailed exercise-testing protocol, criteria for a valid test, or the handling of measurements that were unavailable.

7. Results Posted in the Registry

• Macitentan: mean -0.16 versus -0.67 on control; difference 0.51 (95% CI -0.41 to 1.43), standardized effect d = 0.18; z-test p = 0.279.

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.

Change From Baseline in Peak VO2 Up to Week 52

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Macitentan: mean -0.31 versus -0.92 on control; difference 0.61 (95% CI -0.21 to 1.43), standardized effect d = 0.25; z-test p = 0.143.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Macitentan and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Mean Count Per Minute of Daily Physical Activity Measured by Accelerometer (PA-Ac) Up to Week 16

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Macitentan: mean -3.02 versus -14.34 on control; difference 11.32 (95% CI -26.81 to 49.45), standardized effect d = 0.11; z-test p = 0.561.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Macitentan and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes broaden the description of exercise capacity and daily activity beyond the primary Week 16 endpoint. They include peak VO2 through Week 52 and mean daily physical activity through Week 16, alongside safety outcomes and measures of blood pressure, pulse rate, and oxygen saturation. The overall pattern in the posted continuous secondary comparisons is uncertain: the recalculated confidence intervals for the two displayed comparisons span zero. These outcomes therefore do not provide a clearly resolved statistical contrast that changes the interpretation of the primary result.

Secondary outcomes can help show whether the primary finding is accompanied by a consistent pattern across related measures or follow-up periods. They are not substitutes for the prespecified primary endpoint, because they may use different time points, measurement scales, analysis populations, or statistical models. A result at a later time point does not automatically confirm or contradict a result at an earlier time point. The registry record does not provide enough detail to establish a formal hierarchy among these outcomes.

Multiplicity matters because repeated testing across many outcomes can increase the chance of a nominally notable result arising by chance. The registry lists 26 posted secondary outcomes. If their results are interpreted one at a time without adjustment or a prespecified hierarchy, their evidential weight is lower than a single primary analysis designed to answer the central study question. No multiplicity adjustment is reported in the registry record. Accordingly, secondary results are best treated as supportive or exploratory descriptions, not as independent confirmation of efficacy.

The registry also lists adverse-event and physiological outcomes. Those serve different purposes from exercise-capacity endpoints and should be interpreted using their own definitions and denominators. Their presence broadens the record’s account of outcomes but does not remove the uncertainty in the primary comparison. The statistical analysis plan, any planned secondary-endpoint testing order, and adjustments for multiple comparisons are not reported in the registry record.

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

• Change From Baseline in Peak VO2 Up to Week 52
• Change From Baseline in Mean Count Per Minute of Daily Physical Activity Measured by Accelerometer (PA-Ac) Up to Week 16
• Number of Participants With Treatment-emergent Serious Adverse Events (SAEs)
• Number of Participants With Treatment-emergent Adverse Events (AEs)
• Number of Participants With AEs Leading to Premature Discontinuation of Study Treatment
• Change From Baseline in Systolic and Diastolic Arterial Blood Pressure (BP)
• Change From Baseline in Pulse Rate
• Change From Baseline in Oxygen Saturation (SpO2)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, so the main summaries are group means and measures of spread, followed by a comparison of mean change between randomized groups. The registry reports the placebo mean as -0.67 mL/kg/min and its standard deviation as 2.657; for macitentan, the mean is -0.16 and the standard deviation is 2.855. Standard deviation describes variation among participant measurements around a group mean. It is not the same as a confidence interval, which describes uncertainty about an estimated quantity.

What does the unadjusted comparison represent?

The recalculated mean difference of 0.51 mL/kg/min is the macitentan group mean minus the placebo group mean, based on the posted group summaries. This is an unadjusted comparison: it does not use participant-level covariates or reproduce the sponsor’s ANCOVA model. The recalculated p-value is 0.279. In general, a p-value measures how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

The recalculation is a simple summary-statistic check rather than a substitute for the reported trial analysis. The registry does not give enough information to reconstruct the sponsor’s full model, including its covariates, assumptions, or missing-data handling. As a result, differences between the sponsor estimate and the unadjusted recalculation should not be attributed to any particular adjustment or modeling choice without further documentation.

Why report ANCOVA?

ANCOVA, or analysis of covariance, compares outcome values while accounting for specified covariates. In general, adjustment can improve precision when covariates are chosen appropriately and are related to the outcome. It can also make the estimated comparison conditional on the model and covariates used. The registry reports an ANCOVA analysis with a median unbiased estimate and repeated confidence interval. The covariates and implementation details are not reported in the registry record, so the exact model cannot be assessed from the posted description alone.

The sponsor’s estimate is 0.62 mL/kg/min, with a 99% repeated confidence interval from -0.62 to 1.85. A repeated confidence interval is associated with a specified analysis procedure and coverage level; it should be interpreted according to that procedure rather than assumed to be identical to the interval from a simple unadjusted calculation. The reported p-value is 0.193. The interval includes zero, and the reported test does not establish a clear difference at conventional significance levels. The record does not state the prespecified significance threshold for the sponsor’s primary analysis.

What does the trial design contribute?

Randomization is intended, in general, to balance prognostic factors across groups on average and to support a causal comparison under appropriate conduct and analysis. A placebo-controlled parallel design compares groups followed under different assigned treatments. Double-blinding can reduce some sources of bias, while the registry’s quadruple-masking label indicates a masking classification without specifying the masked roles in this record summary. Randomization and masking do not eliminate all possible bias: adherence, outcome availability, measurement procedures, and analysis choices also matter.

The primary analysis population is described as the full analysis set, including all randomized participants. This definition supports an analysis based on assigned groups, but the registry does not specify in the record summary how participants with missing Week 16 measurements were handled. The posted primary group sizes are 69 and 68. The record does not report a detailed participant flow or reasons why outcome measurements may not have been available.

Why can over-dispersion matter?

General statistical explanation: for a continuous outcome, greater variation relative to the size of a group makes the estimated mean difference less precise. In event-count outcomes, over-dispersion means that variability exceeds what a simple model assumes; ignoring it can make uncertainty look too small. The posted primary standard deviations, 2.657 and 2.855, describe the observed spread for peak VO2 change. The registry does not report a specific over-dispersion assessment for the primary endpoint, and an event-count model is not the method used for this continuous primary comparison.

The physical-activity outcome illustrates why spread and uncertainty matter. Its posted mean changes were -14.34 and -3.02 counts per minute, while the standard deviations were 117.6 and 92.44. The observed variability is large relative to the mean changes, and the recalculated confidence interval for the group difference spans zero. This description does not imply that any particular model assumption was violated; a formal assessment is not reported in the registry record.

How should secondary tests be viewed?

The registry lists 26 posted secondary outcomes, and the trial lists 27 outcome measures overall. When many outcomes are examined, the chance of at least one apparently notable result can increase if each is judged separately without accounting for multiplicity. General approaches include prespecifying a hierarchy, adjusting significance thresholds, or treating secondary analyses as exploratory. The registry record does not report a multiplicity procedure or a hierarchy for interpreting secondary endpoints. Therefore, unadjusted secondary p-values should not be treated as confirmatory evidence by themselves.

The primary and secondary outcome definitions also differ in follow-up time, scale, or analysis summary. Peak VO2 through Week 52 is reported as a least-squares mean with standard error, whereas the Week 16 primary outcome is reported as a mean with standard deviation. A standard error describes uncertainty in an estimated mean; a standard deviation describes participant-level variability. These quantities are not interchangeable. The record’s statistical analysis plan and further model details are not reported in the registry record, limiting independent assessment of all analysis assumptions.

11. Confidence Intervals and Precision

Precision is about how narrowly an estimate is determined by the data and analysis. A confidence interval gives a range of values compatible with the observed data under the model and interval procedure. Narrower intervals generally indicate greater precision; wider intervals indicate more uncertainty. The interval should not be read as a range containing a known true value with certainty, nor as a probability statement about the observed estimate.

For the sponsor’s ANCOVA analysis of the primary endpoint, the estimate was 0.62 mL/kg/min and the 99% repeated confidence interval ran from -0.62 to 1.85. Because the interval includes zero, the reported data do not exclude no difference under that analysis. The positive and negative values within the interval also indicate that effects in either direction remain compatible with the reported analysis. The range is broad enough that the record does not resolve the size or direction of the between-group difference with high precision.

The unadjusted recalculation also has an interval spanning zero, with an estimate of 0.51 mL/kg/min. It is a different calculation from the sponsor’s adjusted analysis and should be read as a descriptive reanalysis of group summaries. The recalculated p-value is 0.279. Neither the point estimate nor the p-value should be interpreted without considering the interval and the assumptions of the analysis.

For the secondary outcomes, the recalculated intervals also span zero. The physical-activity estimate has a relatively wide interval in relation to its point estimate, reflecting considerable uncertainty in that comparison. The Week 52 peak VO2 comparison likewise has an interval that includes zero. These intervals do not establish equivalence, and no equivalence margin is reported in the registry record.

Precision depends on outcome variability, the amount of available information, and the analysis model. The record does not report a clinical-importance threshold for peak VO2 or a precision target for the original design. Thus, the statistical intervals can describe uncertainty around the estimates, but they cannot alone determine whether the estimates are clinically important.

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 planning figures are illustrations based on observed effects, not the original trial’s design calculations. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each scenario asks how many participants per arm would be needed to detect the stated fraction of the observed effect under those assumptions. The original study’s sample-size assumptions and justification are not reported in the registry record.

For the primary Week 16 peak VO2 comparison, planning for 100% of the observed effect gives 459 participants per arm for 80% power and 615 participants per arm for 90% power. Planning for 75% of the observed effect gives 816 participants per arm for 80% power and 1,092 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,836 participants per arm for 80% power and 2,457 participants per arm for 90% power.

In plain language, 80% power describes the chance of detecting an effect of the specified size under the planning assumptions if that effect were the true effect; 90% power describes a higher chance of detection under the same assumptions. The higher-power target requires more participants. Smaller effects also require more participants to distinguish them from random variation with the same planned power. The figures are per arm, not total participants or total events. These are planning illustrations, not observed power, and they should not be mistaken for evidence about the study’s actual power or the result of its analysis.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.510; pooled standard deviation σ = 2.757.
2. n = 2 × (1.96 + 0.842)² × 2.757² / 0.510² = 458.8, rounded up to 459 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
delta <- 0.51                      # observed difference in means
sigma <- 2.75704458916911                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3153137)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 459 (80% power), 615 (90% power)
 75% of observed effect: n per arm = 816 (80% power), 1,092 (90% power)
 50% of observed effect: n per arm = 1,836 (80% power), 2,457 (90% power)
power.t.test: 459.7 
Simulated power at n = 459 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 primary analysis is reported as an ANCOVA, with a median unbiased estimate of 0.62 mL/kg/min and a 99% repeated confidence interval from -0.62 to 1.85. The reported p-value is 0.193. The recalculated comparison from the posted group means is unadjusted: it gives a difference of 0.51 mL/kg/min, a confidence interval that spans zero, and a p-value of 0.279.

These estimates arise from different analysis approaches. The sponsor’s ANCOVA result is the analysis reported by the registry, while the recalculation uses only the posted group means, standard deviations, and group sizes. The registry record does not describe the covariates or full model specification needed to reproduce the sponsor’s estimate. It is therefore not possible to identify from this record alone why the estimates differ, and the simple recalculation should not be presented as a replacement for the sponsor’s model.

Both analyses have confidence intervals that include zero. This shared feature indicates that neither result precisely rules out no between-group difference. It does not establish that the groups are equivalent, and the registry does not report an equivalence margin. The sponsor’s estimate and the unadjusted recalculation should be read in light of their respective methods, populations, and uncertainty rather than treated as interchangeable results.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a trial examines several outcomes, time points, or comparisons. In general, if each test is judged against a nominal threshold without accounting for the number of tests, the chance of at least one false-positive finding can rise. A protocol may address this through a prespecified hierarchy, adjusted significance levels, or a distinction between confirmatory and exploratory analyses. The registry lists 27 outcome measures, including 26 posted secondary outcomes, but a multiplicity strategy is not reported in the registry record.

The registry does not report the original statistical analysis plan, a prespecified order for testing secondary outcomes, or whether any adjustment was used for multiple comparisons. Consequently, the secondary outcomes should not be treated as a set of independent confirmatory tests. Their findings can inform the overall description of the trial, but unadjusted comparisons carry less weight than a primary result evaluated according to a documented testing plan.

Missing-data handling is also important for a change-from-baseline endpoint. The primary population is defined as the full analysis set, including all randomized participants. The posted primary group sizes are 69 for placebo and 68 for macitentan. The registry record does not report how participants without a Week 16 measurement were handled, whether imputation was used, or whether sensitivity analyses assessed the effect of missing outcomes. The record also does not provide reasons for missing measurements or a detailed participant flow in the information summarized for this analysis.

The secondary physical-activity outcome has posted group sizes of 58 and 61, while the primary groups have posted sizes of 69 and 68. This indicates that the reported outcome summaries use different numbers of participants, but the reasons and missing-data methods are not reported in the registry record. Differences in outcome availability can affect precision and may affect interpretation if availability is related to participant characteristics or outcomes.

The trial’s original sample-size justification, interim-analysis plan, and detailed statistical plan are not reported in the registry record. Their absence prevents assessment of whether the final sample met the original precision or power target, whether interim monitoring affected the analysis, and how deviations from planned methods were handled. These unknowns should remain explicit rather than being filled by assumptions.

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: atrial flutter (1.5%), cardiac arrest (1.5%), supraventricular tachycardia (1.5%), non-cardiac chest pain (1.5%), appendicitis (1.5%).

The registry reports treatment-emergent serious adverse events for 9 of 69 participants in the placebo group and 13 of 68 participants in the macitentan group. It reports other treatment-emergent adverse events for 18 of 69 participants with placebo and 15 of 68 with macitentan. No deaths were reported in either group. These are participant counts, not counts of every event episode, and the record’s summary does not establish that an event was caused by assigned treatment.

The serious-event terms listed in the record include atrial flutter, cardiac arrest, supraventricular tachycardia, non-cardiac chest pain, appendicitis, and bronchitis, each reported as 1.5%. The registry’s listed percentages describe the reported terms; they do not by themselves establish comparative risks for individual events. The record does not provide enough detail in this summary to assess event timing, severity beyond the serious classification, or causal attribution.

Safety counts should be read alongside the number of participants at risk and the duration and completeness of follow-up, which are not fully detailed in this summary. Rare events are difficult to characterize precisely from a trial of this size. The counts are descriptive and should not be converted into claims that a treatment is safe or unsafe.

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

The primary result describes change in peak oxygen uptake through Week 16 among participants assigned to macitentan or placebo. The posted mean changes were -0.16 mL/kg/min and -0.67 mL/kg/min, respectively. The sponsor’s ANCOVA estimate was 0.62 mL/kg/min, and its 99% repeated confidence interval included zero. The unadjusted recalculation also produced an interval that included zero. Together, these results indicate that the registry record does not precisely establish the direction or size of a between-group difference in the primary endpoint.

That interpretation is not the same as saying there was no effect. An interval that includes zero can be compatible with no difference and with nonzero differences within the interval. Nor does it establish equivalence: equivalence requires a prespecified margin and an analysis designed to evaluate it, and such a margin is not reported in the registry record. A non-significant result is not proof that treatments have identical effects.

The observed estimates also do not, by themselves, determine clinical importance. The record does not report a threshold for a meaningful change in peak VO2. Statistical significance, effect size, precision, and clinical relevance are distinct considerations. A numerical difference can be estimated without establishing whether it is important to participants, and an uncertain estimate can leave a range of potentially relevant effects unresolved.

The secondary outcomes add information about other follow-up periods and measures, but their unadjusted comparisons should be interpreted cautiously because a multiplicity procedure is not reported. The safety counts describe participants with reported events; they do not establish causation or provide a complete account of all possible risks. The registry record does not report the original sample-size rationale, detailed missing-data methods, or full statistical analysis plan, so those aspects of the evidence cannot be evaluated from this record summary.

The conclusions should therefore remain tied to the registered outcomes and analyses: the posted data show group summaries and an uncertain primary comparison, with additional descriptive secondary and safety results. They do not support a broad claim about all participants with Fontan palliation, all follow-up periods, or outcomes not measured in the trial.

18. Why This Trial Matters Statistically

This trial raises several important statistical issues in a setting where the primary outcome is a continuous exercise-capacity measure. Reporting both group means and standard deviations makes the scale and variability visible, while a between-group estimate and confidence interval communicate the uncertainty in the comparison. The interval matters as much as the point estimate: the sponsor’s 99% interval includes zero and allows a range of effects in either direction.

The contrast between the sponsor’s ANCOVA analysis and the unadjusted recalculation also illustrates why analysis methods need to be distinguished. Adjusted and unadjusted estimates can differ because they answer the comparison using different statistical procedures. Without the model details, a reader cannot reproduce the sponsor’s result or determine the source of the difference. Clear reporting of covariates, assumptions, and missing-data methods would help make the analysis more assessable.

Multiple outcomes are another central consideration. The registry lists many secondary measures, including another peak VO2 time point and physical activity. These outcomes may add useful context, but interpretation depends on knowing which analyses were confirmatory and how multiple testing was handled. That information is not reported in the registry record, so isolated secondary findings warrant restraint.

The planning illustrations show how strongly sample requirements depend on the effect size targeted and the desired power. They are not evidence of the trial’s observed power and do not reveal the original design rationale. Distinguishing an illustrative calculation from the trial’s actual planning is essential when discussing whether a study was sized to detect a particular effect.

Finally, the record’s safety counts emphasize the difference between descriptive event reporting and causal inference. Counts should be understood with denominators, follow-up, and uncertainty, and not treated as definitive evidence about uncommon events. These issues make transparent reporting of analysis plans, missingness, and event definitions important for interpreting randomized clinical trials.

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 registry record does not report the original sample-size justification or the assumptions used in the trial’s design. The planning illustrations are based on observed effects and should not be used to infer the trial’s planned power. The original statistical analysis plan and interim-analysis plan are also not reported, limiting assessment of prespecified methods and any planned monitoring.

For the primary endpoint, the sponsor’s ANCOVA model is not described in enough detail to reproduce it. The covariates, model assumptions, and handling of missing outcomes are not reported in the registry record. Although the full analysis set is defined as all randomized participants, the record does not explain the availability of Week 16 measurements or how missing data were addressed. The secondary physical-activity summaries have fewer participants than the primary summaries, and reasons for that difference are not reported.

The registry lists many outcomes, but a multiplicity strategy is not reported. This makes it difficult to distinguish confirmatory secondary tests from exploratory analyses or to evaluate the evidential weight of individual secondary findings. In addition, the primary endpoint is measured through Week 16, while a secondary peak VO2 outcome extends through Week 52; the different time points should not be treated as interchangeable.

The record summary does not provide a clinical-importance threshold for peak VO2, detailed eligibility criteria, participant characteristics, full participant flow, or a detailed account of measurement procedures. The safety summary is also limited: counts of participants with events do not describe event timing or establish causality. These limitations do not invalidate the posted results, but they constrain what can be inferred from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Study Assessing the Efficacy and Safety of Macitentan in Fontan-palliated Subjects — NCT03153137.
• Registry record last updated 2025-03-30; status last verified 2025-03.
• Results first posted 2022-09-13.
• 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

The registry record describes a completed Phase 3 randomized, double-blind, placebo-controlled, parallel-group study of macitentan 10 mg per day in Fontan-palliated adult and adolescent participants. Enrollment was 142. The primary endpoint was change from baseline in peak VO2 through Week 16, analyzed in the full analysis set.

The posted primary group means were -0.67 mL/kg/min for placebo and -0.16 mL/kg/min for macitentan. The sponsor reported an ANCOVA estimate of 0.62 mL/kg/min with a 99% repeated confidence interval from -0.62 to 1.85. The unadjusted recalculation also has a confidence interval spanning zero. Secondary and safety outcomes provide additional descriptive information, with uncertainty and interpretive limits.

The registry record does not report the original sample-size justification, full statistical analysis plan, multiplicity procedure, or detailed missing-data methods. These omissions limit independent assessment of the planned analyses and the precision or generalizability of the findings.