Efficacy and Tolerability of Subcutaneously Administered Treprostinil Sodium in Patients With Severe (Non-operable) Chronic Thromboembolic Pulmonary Hypertension (CTREPH): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Tolerability of Subcutaneously Administered Treprostinil Sodium in Patients With Severe (Non-operable) Chronic Thromboembolic Pulmonary Hypertension (CTREPH) (NCT01416636), a randomized phase 3 study. The primary outcome is Change in 6-minute Walk Test Distance After 24 Weeks.

2. Clinical Question

This was a comparison between two dose regimens of the same study drug, not a comparison with a placebo or an untreated group. The central statistical question is therefore about the difference between the groups as assigned and analyzed in this trial. The posted results show average changes and a group contrast, but those summaries do not by themselves establish the clinical importance of a particular change. The registry record does not report a threshold defining a clinically important difference in walking distance.

3. Trial Design

The registry describes CTREPH as a phase 3, randomized, quadruple-masked, parallel-group clinical study. It lists 105 enrolled participants and two treatment arms: high-dose and low-dose subcutaneous treprostinil sodium. The study is marked completed. The registry record lists the start as 2009-03 and primary completion as 2016-11.

Both groups received treprostinil sodium; the contrast was between dose strategies. The low-dose arm description states that the dose was escalated to an approximate target of 3 ng/kg/min after the first 12 weeks and then kept stable for another 12 weeks. It also notes that the predefined infusion-rate schedule could lead to an interim dose of up to 6 ng/kg/min. The high-dose arm description repeats some of this wording and is truncated. Its complete intended schedule is not reported in the registry record, so the precise distinction between the regimens cannot be fully reconstructed from those descriptions.

The primary endpoint population is described as all randomized participants who received at least one dose of study medication. The posted primary arm summaries include 53 participants in the high-dose group and 52 in the low-dose group. The registry record does not report the randomization procedure, allocation concealment details, or the original sample-size justification. It also does not explain the masking roles meant by “quadruple” in the registry entry.

The study planned measurement of the six-minute walk test at baseline and 24 weeks. The record states that, when values were missing, last-observation-carried-forward imputation was used and Visit 4 (day 84) values were used in those cases. The extent and pattern of missing primary outcome data are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: All randomized subjects who received at least one dose of study medication.

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 in 6-minute Walk Test Distance After 24 Weeks, measured over Baseline and 24 weeks.

The primary endpoint is change in six-minute walk test distance from baseline to 24 weeks, measured in meters. The six-minute walk test records how far a participant can walk during a fixed test period. As a continuous measure, it retains information about the amount of change rather than reducing results to categories such as improved or not improved. The registry specifies that the outcome is summarized as a mean with a standard deviation.

Walking distance is used in this trial as a functional measure in people with severe non-operable chronic thromboembolic pulmonary hypertension. Comparing changes between randomized groups asks whether the average change differed under the two dose strategies during the study period. A group mean is an average, however, and does not describe every participant’s experience or the spread and shape of individual outcomes. The standard deviations help convey variability among participants.

The registry identifies baseline and 24 weeks as the measurement timeframe. For missing values, it states that last-observation-carried-forward imputation was used, using values recorded at Visit 4 (day 84) in such cases. This means the posted endpoint is not necessarily based only on measurements obtained at the 24-week visit. The number of participants whose values were imputed, and the effects of alternative missing-data assumptions, are not reported in the registry record.

The endpoint provides a functional outcome for comparing the groups, but interpretation also depends on the estimated size and precision of the difference, as well as its clinical context. A statistical test alone does not determine whether a difference is important to patients.

7. Results Posted in the Registry

• Low Dose: mean 3.83 versus 45.43 on control; difference -41.60 (95% CI -66.13 to -17.07), standardized effect d = -0.65; 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 Clinical Worsening

• 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:
  • Low Dose: 23.1% (12/52) versus 13.2% (7/53) on control; risk difference 9.9 percentage points (95% CI -4.8 to 24.5), risk ratio 1.75 (0.75–4.09); unadjusted two-proportion z-test p = 0.189.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose and the control. The interval gives the range of effects that remain compatible with the data.

Effect on Maximal Borg Score During 6-minutes Walk Test

• 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:
  • Low Dose: mean -0.13 versus -0.44 on control; difference 0.31 (95% CI -0.62 to 1.24), standardized effect d = 0.13; z-test p = 0.513.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose and the control. The interval gives the range of effects that remain compatible with the data.

Effect on Quality of Life by the MINNESOTA Questionnaire

• 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:
  • Low Dose: mean -4.63 versus -6.36 on control; difference 1.73 (95% CI -6.73 to 10.19), standardized effect d = 0.08; z-test p = 0.688.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover clinical worsening, maximal Borg score during the walk test, quality of life by the Minnesota Questionnaire, and additional outcomes listed in the registry, including functional class, N-terminal Pro-BNP, and hemodynamic measures. The available posted analyses do not all point to a clear between-group difference. This broad pattern should be read alongside, rather than substituted for, the primary walking-distance comparison: the measures address different dimensions and may have different precision.

The secondary outcomes are not simply supporting replications of the primary endpoint. Clinical worsening is a participant count, while the Borg score and quality-of-life score are continuous measures; the other listed outcomes include different clinical and hemodynamic measures. A result on one outcome need not match a result on another. Also, the registry lists 11 secondary outcomes, but results for all of them are not represented in the posted secondary results described in the record.

Unadjusted secondary analyses carry less weight when many outcomes or tests are examined. In general, making multiple comparisons increases the chance that at least one result will appear statistically notable by chance, even when each individual test is conducted as planned. The registry record does not report a multiplicity adjustment, testing hierarchy, or complete prespecified analysis plan. Therefore, secondary p-values should be considered exploratory unless their place in a prespecified inferential plan is documented. They do not overturn or confirm the primary finding on their own.

The results also have differing amounts of information, reflected in their group sizes and uncertainty. A non-significant result does not prove that the groups are equivalent, particularly when its interval remains compatible with effects in either direction. Conversely, a nominally notable secondary result would not establish a reliable effect without attention to multiplicity, precision, and the analysis plan.

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

• Number of Participants With Clinical Worsening
• Effect on Maximal Borg Score During 6-minutes Walk Test
• Change in WHO/NYHA (World Health Organization - New York Heart Association) Functional Class
• Effect on Quality of Life by the MINNESOTA Questionnaire
• Effect on N-terminal Pro-BNP Levels
• Effect on Hemodynamic Parameter (PVR - Pulmonary Vascular Resistance)
• Effect on Hemodynamic Parameter (CI - Cardiac Index)
• Effect on Hemodynamic Parameter (CO - Cardiac Output)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent?

A mean summarizes the average value in a group. For this primary endpoint, the arm summaries are mean changes in walking distance, expressed in meters. A mean difference compares the two group means. In the re-calculation, the contrast is defined as low dose minus high dose, so a negative estimate corresponds to a lower mean change in the low-dose arm. This sign convention is important: reversing the order of subtraction would reverse the sign without changing the substantive group comparison.

The re-calculated contrast is a simple, unadjusted comparison based on the posted arm-level summary statistics. It is not the same as a model-based adjusted analysis. The registry reports an ANCOVA result but does not post the adjusted estimate, confidence interval, or full model specification. The simple comparison is useful for interpreting the arm summaries, while the sponsor’s reported analysis addresses the trial’s comparison using the stated method.

What do the standard deviations and standard errors describe?

A standard deviation describes how spread out participant outcomes are within a group. It is not the uncertainty of the group mean itself. A standard error describes the sampling uncertainty of an estimate, such as a mean. In general, the standard error depends on both outcome variability and the amount of information available; it is not a measure of how widely individual outcomes differ. The posted primary results give standard deviations for each arm, and the simple re-calculation uses the pooled standard deviation for its standardized summary.

Standardizing a mean difference expresses the group contrast relative to a measure of variability. This can help compare effects measured on different scales, but it does not replace the original clinical units. The registry does not report a threshold for interpreting a standardized effect as clinically important, so the estimate in meters remains central to understanding the primary outcome.

What does a confidence interval add?

A confidence interval is a range of values compatible with the data and the statistical method used, under its assumptions. It conveys precision and the range of plausible effects more directly than a p-value alone. A narrow interval indicates greater precision than a wide interval, all else equal. An interval that includes zero is compatible with no group difference under that method; an interval excluding zero indicates that zero is not among the values in that interval. This statistical interpretation does not settle clinical importance.

The re-calculated interval is for the simple unadjusted contrast, not the sponsor’s ANCOVA estimate. It should be read together with the method that produced it. The registry reports p-values for the sponsor analyses but no corresponding confidence intervals or adjusted effect estimates for those analyses.

Why are different tests reported?

ANCOVA is a regression-based method that compares groups while accounting for one or more covariates. The registry names ANCOVA for the primary comparison but does not report which covariates were included, the model details, or whether any assumptions were checked. Those details are not reported in the registry record.

The Wilcoxon (Mann-Whitney) procedure is a rank-based comparison. In general, it assesses whether values in one group tend to be higher or lower than values in another, using ranks rather than comparing means directly. It is not simply another calculation of the mean difference. The registry reports the test and p-value but does not provide a rank-based effect estimate or confidence interval. Agreement in the direction of statistical evidence across different methods can be informative, but the tests answer related rather than identical statistical questions.

Why can over-dispersion matter?

For count or binary outcomes, a statistical model may assume a particular amount of variation. Over-dispersion means the observed variation is greater than that assumed by a model. If ignored, uncertainty can be understated and statistical evidence can appear stronger than warranted. This is a general statistical concern, not a finding reported for this study. The registry record does not report an over-dispersion assessment or a model-based adjustment for the secondary clinical-worsening comparison.

For the primary continuous endpoint, variation is represented by the standard deviations and standard errors in the posted summaries. The simple re-calculation uses those summary statistics and does not account for baseline covariates or other features of the sponsor’s analysis.

How should p-values be read?

A p-value describes how surprising the observed data, or data more extreme, would be under a specified null hypothesis and analysis method. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. The registry reports p-values for ANCOVA and Wilcoxon analyses, and the simple re-calculation reports an unadjusted p-value. Because the analyses use different methods, their p-values should be attributed to their respective procedures rather than treated as interchangeable estimates of effect.

The statistical plan, prespecified testing hierarchy, and any adjustment for examining multiple outcomes are not reported in the registry record. That omission matters especially for secondary analyses, where several outcomes and tests can generate multiple opportunities to observe a small p-value.

11. Confidence Intervals and Precision

The simple unadjusted primary contrast is -41.6 m for low dose relative to high dose, with a 95% confidence interval from -66.13 to -17.07 m. The interval excludes zero and spans negative values of differing magnitude. It therefore indicates statistical evidence of a difference under this re-calculation, while also showing that the exact size of the contrast is uncertain.

A confidence interval is not a guarantee that the true effect lies within its endpoints. Rather, it describes the range of values compatible with the data and the method under repeated-sampling assumptions. The width reflects both the observed variability and the amount of information in the groups. Here the interval pertains only to the unadjusted summary-statistic comparison; it is not a confidence interval from the sponsor’s ANCOVA analysis.

The sponsor analyses are reported with p-values but without an effect estimate or confidence interval. Consequently, their statistical significance can be read from the posted p-values, but the registry does not allow the precision of the sponsor’s adjusted effect estimate to be assessed directly. A p-value does not indicate how large the group difference is or how narrowly it has been estimated.

Precision also differs across outcomes and should not be inferred from one result to another. Secondary outcomes have their own participant counts, variability, and estimates. For several secondary comparisons, the confidence intervals in the recalculations span values on both sides of zero, reflecting substantial uncertainty about the direction and size of the contrast. The registry record does not report a clinical-importance threshold for the primary walking-distance outcome, so statistical precision alone cannot determine whether a particular value in the interval would be important in practice.

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 effects, not the original enrollment plan. For these comparisons, the figures are participants per arm; the record’s general planning note says time-to-event tables, if present, give total events, while other planning tables give participants per arm. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect.

The 80% power column gives the estimated number of participants per arm for a planning scenario designed to have an 80% chance of detecting the specified effect, if the assumptions used for that calculation hold. The 90% power column gives the corresponding planning number for a 90% chance. These are design-planning probabilities under assumptions, not guarantees about a future study’s result. This is not observed power.

The rows consider the full observed effect and smaller fractions of that effect. Smaller effects need more participants to detect under the same planning assumptions, which is why the participant requirements increase as the assumed effect becomes smaller. The calculations use effects estimated from this trial, so they should not be mistaken for an independent estimate of the effect likely in a new study. In particular, an observed effect can be imprecise and may not be the effect a future trial should target.

The registry record does not report the original sample-size justification or the assumptions used to choose the enrolled sample. These illustrations answer a different question: what sample sizes follow from the stated planning assumptions and an effect based on the posted results. They should be read as planning aids rather than as evidence about the adequacy of the completed trial.

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 = -41.600; pooled standard deviation σ = 64.267.
2. n = 2 × (1.96 + 0.842)² × 64.267² / -41.600² = 37.5, rounded up to 38 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 <- -41.6                      # observed difference in means
sigma <- 64.267002381826                     # 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(1416636)
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 = 38 (80% power), 51 (90% power)
 75% of observed effect: n per arm = 67 (80% power), 90 (90% power)
 50% of observed effect: n per arm = 150 (80% power), 201 (90% power)
power.t.test: 38.4 
Simulated power at n = 38 per arm: 0.796 (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 registry reports two sponsor analyses for the primary comparison: ANCOVA with p = 0.002 and Wilcoxon (Mann-Whitney) with p < 0.001. The record does not post the sponsor’s adjusted effect estimate or confidence interval for either analysis. The simple re-calculation from the arm summaries gives a low-dose-minus-high-dose mean difference of -41.6 m, with a 95% confidence interval from -66.13 to -17.07 m and p < 0.001.

The re-calculation is unadjusted and should be understood as a supplementary check of the posted summary statistics, not a replacement for the sponsor’s trial analysis. The reported sponsor analyses and the re-calculation point to evidence of a difference between groups, but the methods are not identical and their effect estimates should not be conflated. The ANCOVA result may account for covariates, but which covariates were used and the model details are not reported in the registry record.

The record does not flag a discrepancy between the posted summaries and the sponsor’s analyses. The sponsor’s own analysis therefore remains the primary reported analysis, while the re-calculation helps translate the arm summaries into an unadjusted contrast and an associated interval. Neither p-value alone nor the unadjusted interval establishes clinical importance.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, comparisons, or analysis methods are examined. Each additional test creates another opportunity for a result to appear statistically notable by chance. Methods such as prespecifying a hierarchy of outcomes or adjusting the significance threshold can help control this issue. The registry lists a primary outcome, multiple secondary outcomes, and more than one analysis for the primary comparison. Whether the trial used an adjustment, a prespecified testing order, or another multiplicity strategy is not reported in the registry record.

The primary outcome is distinguished in the record, which helps identify the main question, but the full statistical analysis plan is not reported. The registry does not specify whether the reported ANCOVA and Wilcoxon tests were both prespecified, whether one was primary and the other a sensitivity analysis, or how the secondary comparisons fit into a testing hierarchy. Without those details, secondary p-values should not be interpreted as if they were all confirmatory tests with controlled overall error.

Missing-data handling is partly described. The registry states that last-observation-carried-forward imputation was used for missing primary endpoint values, using Visit 4 (day 84) values in such cases. This approach carries an earlier recorded value forward to represent a later assessment. As a general statistical matter, it relies on an assumption that the carried-forward value is an adequate substitute for the missing later value. If outcomes would have changed after the last observed visit, the imputed value may not reflect the unobserved outcome. The registry does not report the number of imputed values, reasons for missingness, or sensitivity analyses using alternative assumptions.

The endpoint population is described as randomized participants who received at least one dose of study medication. The record does not report whether participants who did not receive a dose were excluded from the endpoint analysis or how they were handled in other analyses. Details of an intention-to-treat analysis, protocol deviations, and analysis-population definitions beyond the stated endpoint population are not reported in the registry record. These omissions limit assessment of whether the analysis preserved all the protections of randomization and how sensitive the findings are to missing data and analysis choices.

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: right ventricular failure (11.3%), cardiac failure (3.8%), dyspnea (1.9%), syncope (1.9%), diarrhoea (1.9%).

The posted safety figures count participants affected, with separate counts for serious adverse events, other adverse events, and deaths. In the high-dose group, 9 of 53 participants were recorded as affected by a serious adverse event, 53 of 53 by another adverse event, and 2 deaths were reported. In the low-dose group, the corresponding figures were 10 of 52, 51 of 52, and 1 death.

The registry also lists serious adverse event terms and percentages, including right ventricular failure at 11.3%, cardiac failure at 3.8%, and dyspnea, syncope, diarrhoea, and nausea each at 1.9%. These terms are listed in the record without arm-specific breakdowns in the posted summary, so they should not be assigned to a particular dose group from these figures alone.

These counts describe events reported during the study; they do not establish that study medication caused an event. The registry summary does not provide event timing, severity details beyond the serious-event designation, exposure-adjusted rates, or a statistical comparison of safety outcomes. Small group counts also make simple numerical differences difficult to interpret in isolation. Safety findings should be read as descriptive reporting rather than as proof of causation or a definitive comparison of risk.

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

The primary result is evidence of a difference in mean change in six-minute walk distance between the high- and low-dose groups over the stated 24-week period. The posted arm summaries and the simple unadjusted contrast indicate a larger mean change in the high-dose group. The sponsor’s reported ANCOVA and Wilcoxon analyses also report statistical evidence of a difference. These findings address the comparison made within this randomized trial.

They do not establish the clinical importance of the difference. The registry record does not state a threshold for a meaningful change in walking distance, and statistical significance is not a substitute for such a threshold. The mean also does not show how individual participants’ outcomes were distributed or whether the group averages describe every participant’s experience.

The comparison is between two treprostinil sodium dose regimens, not between treatment and no treatment. It therefore does not estimate the effect of treprostinil sodium versus no study drug. The arm descriptions are incomplete and partly overlapping in wording, particularly for the high-dose arm, so the precise regimen contrast cannot be fully reconstructed from the registry descriptions.

The results are limited to the enrolled study population, the reported endpoint definition, and the follow-up period. The record describes last-observation-carried-forward imputation for missing primary endpoint values but does not give the number of imputed values or sensitivity analyses. The registry also does not report the complete statistical analysis plan, details of the ANCOVA model, or a multiplicity strategy. These gaps make it harder to evaluate how robust the reported estimates are to analysis choices.

Finally, the posted secondary outcomes and safety counts provide additional descriptive context, but they do not turn the primary result into a complete assessment of every clinical outcome. The available record supports a statistical comparison of the two assigned groups; it does not support conclusions about every possible dose, population, duration, or outcome.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can answer a focused question while still requiring careful attention to what the contrast represents. Since both groups received treprostinil sodium, the primary estimate compares dose strategies rather than treatment against no treatment. That distinction determines the scope of the conclusion and prevents a group difference from being interpreted as an estimate of the drug’s effect versus no therapy.

It also shows why an effect estimate and its interval are more informative than a p-value alone. The simple re-calculation expresses the group contrast in meters and gives a range of values compatible with that unadjusted analysis. The sponsor’s reported p-values indicate statistical evidence under named methods, but without the sponsor’s effect estimate and confidence interval, the size and precision of that adjusted result cannot be directly assessed from the registry record.

The record also makes analysis choices visible as part of interpretation. The primary endpoint uses an imputation method for missing values, and the registry reports several secondary outcomes and analyses. Missing-data assumptions, multiplicity, and incomplete model details can affect how confidently results are interpreted. These are not technical footnotes: they shape the meaning and reliability of the estimates.

Finally, a completed randomized study can still leave important reporting gaps. The original sample-size justification, complete statistical plan, and full regimen descriptions are not reported in the registry record. Separating the reported sponsor analysis from an unadjusted re-calculation, and distinguishing statistical evidence from clinical importance, gives readers a more transparent account of what the posted data can and cannot resolve.

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 descriptions of the dose arms are incomplete. The low-dose description includes an approximate target of 3 ng/kg/min after the first 12 weeks and a possible interim dose of up to 6 ng/kg/min. The high-dose description repeats similar wording and ends mid-description. The record therefore does not allow a complete reconstruction of the intended difference between the dose regimens.

The primary outcome analysis population is specified as randomized participants who received at least one dose, but the registry does not provide a full account of participants excluded from analyses, protocol deviations, or the handling of participants who may not have received study medication. The number of missing 24-week values and the number treated with last-observation-carried-forward are also not reported. No sensitivity analysis for the missing-data assumption is described.

The sponsor’s primary analysis methods are named, but the ANCOVA covariates and full model specification are not reported. Sponsor effect estimates and confidence intervals are not posted. The unadjusted re-calculation is therefore not a substitute for a complete report of the sponsor’s modeled effect. The original sample-size justification and assumptions, interim analysis plans, and multiplicity procedures are also not reported in the registry record.

The registry lists 11 secondary outcomes, while the available posted secondary results cover only some of them. The clinical-worsening comparison and other secondary analyses should be interpreted cautiously because the testing plan and multiplicity handling are not reported. Safety figures are descriptive and do not include a causal assessment or exposure-adjusted comparison. These limitations concern the completeness of the registry record and do not, by themselves, establish that the trial analyses were improperly conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Tolerability of Subcutaneously Administered Treprostinil Sodium in Patients With Severe (Non-operable) Chronic Thromboembolic Pulmonary Hypertension (CTREPH) — NCT01416636.
• Registry record last updated 2022-06-07; status last verified 2022-05.
• Results first posted 2019-06-10.
• 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

NCT01416636, CTREPH, is a completed phase 3 randomized, quadruple-masked, parallel-group study of subcutaneous treprostinil sodium in severe non-operable chronic thromboembolic pulmonary hypertension. The registry lists 105 enrolled participants and compares high-dose with low-dose regimens.

The primary outcome is change in six-minute walk distance from baseline to 24 weeks. The posted summaries report mean changes of 45.43 m in the high-dose group and 3.83 m in the low-dose group. The simple unadjusted comparison is -41.6 m for low dose relative to high dose, with a 95% confidence interval from -66.13 to -17.07 m. Sponsor analyses report p = 0.002 for ANCOVA and p < 0.001 for Wilcoxon (Mann-Whitney).

The record also lists secondary outcomes and adverse-event counts. Important details, including the full dose descriptions, original sample-size justification, complete statistical plan, and missing-data sensitivity analyses, are not reported in the registry record.