A Study to Investigate the Pharmacokinetic Interactions Between Simeprevir and Ledipasvir in a Treatment Regimen Consisting of Simeprevir, Sofosbuvir, and Ledipasvir in Treatment-naive Participants With Chronic Hepatitis C Virus Genotype 1 Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Investigate the Pharmacokinetic Interactions Between Simeprevir and Ledipasvir in a Treatment Regimen Consisting of Simeprevir, Sofosbuvir, and Ledipasvir in Treatment-naive Participants With Chronic Hepatitis C Virus Genotype 1 Infection (NCT02421211), a randomized phase 2 study. The primary outcome is Minimum Plasma Concentration (Cmin) of Simeprevir (SMV).

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, open-label, parallel study organized into two panels. The registry lists an enrollment of 41 and a completed status. The listed start date is 2015-05-19, and the primary completion date is 2015-11-10. Janssen Sciences Ireland UC is listed as the sponsor. The study purpose was to investigate pharmacokinetic interactions between simeprevir and ledipasvir in regimens that also included sofosbuvir.

The two panels used different treatment sequences. In Panel 1, participants received simeprevir 150 mg with sofosbuvir 400 mg once daily from Day 1 until Day 14, followed by simeprevir with a fixed-dose combination of ledipasvir 90 mg and sofosbuvir 400 mg. The primary results label the Panel 1 measurements as Day 14 and Day 28. The available Panel 1 description is incomplete after its reference to the later regimen, so the full treatment-duration details are not reported in the registry record. Panel 2 is described as receiving ledipasvir 90 mg/sofosbuvir 400 mg from Day 1 until Day 14, followed by simeprevir 150 mg with that fixed-dose combination from Day 15 until Day 56.

Randomization is listed, but the randomization procedure, allocation ratio, and whether participants were randomized between panels are not reported in the registry record. Masking is listed as none, consistent with an open-label study. The parallel model is also recorded, although the posted primary contrast is labeled with sequential Panel 1 regimens and assessment days. The registry record does not explain the relationship between that design label and the within-panel Day 14/Day 28 comparison. These design details matter when deciding how far the numerical contrast can be interpreted as a randomized treatment effect.

The study recorded 20 outcome measures and 6 analyses. The primary posted result concerns simeprevir minimum concentration in Panel 1. The registry also names secondary pharmacokinetic measures, including trough and average concentrations and fluctuation indices for simeprevir and ledipasvir. The numerical secondary results available for discussion cover only some of those measures.

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 41 participants were enrolled in the study, among them 40 participants (20 per panel) were randomized and treated. One participant was early terminated from the study, due to withdrawal of consent before randomization to study drug. All randomized participants received study drug and were included in the intent to treat (ITT) population.

Overall Study

Analysis population for the primary outcome, as defined in the registry: The ITT analysis set is defined as all participants who took at least 1 dose of SMV, LDV, or SOF.

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 Minimum Plasma Concentration (Cmin) of Simeprevir (SMV), measured over Pre-dose, 0.5, 1, 2, 4, 6, 8, 10, 12, 18, and 24 hours post-dose on Day 14 and Day 28.

The primary endpoint is simeprevir minimum plasma concentration, abbreviated Cmin, in nanograms per milliliter. The registry defines Cmin as the minimum observed plasma concentration. Measurements were scheduled pre-dose and at 0.5, 1, 2, 4, 6, 8, 10, 12, 18, and 24 hours post-dose on Day 14 and Day 28. The posted summary gives a mean and standard deviation for each listed Panel 1 condition.

Pharmacokinetic concentration measures describe drug exposure in the body over time. A minimum concentration captures the lowest observed point in a sampling interval; it is distinct from a peak concentration or an average across the interval. In general, such measures can help characterize whether co-administered medicines are associated with changes in exposure. That is the statistical role of this endpoint in a pharmacokinetic interaction study. It is not itself a measure of viral clearance, sustained response, symptoms, or other clinical outcomes.

The analysis population is defined in the registry as the ITT analysis set: all participants who took at least 1 dose of simeprevir, ledipasvir, or sofosbuvir. The primary comparison is labeled as simeprevir plus sofosbuvir on Day 14 versus simeprevir plus ledipasvir/sofosbuvir on Day 28. Because both regimen and assessment day differ in that contrast, the endpoint result describes the posted difference between those conditions; it does not isolate the contribution of ledipasvir from every other possible time-related or regimen-related influence. The registry record does not report a more detailed estimand definition or the statistical method used for its sponsor analysis.

7. Results Posted in the Registry

• Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28): mean 6,701 versus 2,411 on control; difference 4,290 (95% CI 1,821 to 6,759), standardized effect d = 1.08; 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.

Trough Plasma Concentration (Ctrough) of Simeprevir

• 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:
  • Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28): mean 8,453 versus 3,059 on control; difference 5,394 (95% CI 1,984 to 8,804), standardized effect d = 0.98; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Average Plasma Concentration at Steady State (Cavg,ss) of Simeprevir

• 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:
  • Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28): mean 10,139 versus 4,196 on control; difference 5,943 (95% CI 2,287 to 9,599), standardized effect d = 1.03; z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Fluctuation Index (FI) of Simeprevir

• 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:
  • Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28): mean 84.40 versus 144.00 on control; difference -59.60 (95% CI -88.94 to -30.26), standardized effect d = -1.26; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Panel 1: SMV 150mg+LDV 90mg/SOF 400mg (Day 28) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The numerical secondary results available for simeprevir show a generally aligned pattern across the posted measures: the Day 28 condition has higher reported trough and average concentration means than the Day 14 condition, while the fluctuation index is lower. These directions are broadly consistent with the primary result’s higher mean minimum concentration in the Day 28 condition. Together, these measures describe different aspects of plasma exposure; they are not independent confirmations of a clinical outcome.

The secondary endpoints are pharmacokinetic measures, including trough concentration, average concentration at steady state, and fluctuation index. Each captures a different feature of the concentration profile. In general, convergence across related measures can help characterize the exposure pattern, but the measures may be correlated because they arise from the same participants, medicines, and sampling schedules. The registry record does not report how these measures were jointly modeled or whether correlations were incorporated in the analyses.

The record names additional secondary measures for simeprevir and ledipasvir, and lists 14 secondary outcomes as posted. However, the numerical comparisons available for discussion cover only a subset of the named outcomes. Numerical results for other listed measures are not reported in the registry record. The pattern should therefore be understood as a description of the available simeprevir results, not as a complete account of all planned or recorded secondary outcomes.

Unadjusted secondary results carry less weight than a prespecified primary analysis because a study can examine many outcomes and comparisons. In general, testing more hypotheses increases the chance that at least one result appears statistically notable by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary endpoints. Their estimates can inform the pharmacokinetic description, but the associated uncertainty and the number of analyses mean they should not be treated as separate definitive evidence or as substitutes for the primary analysis.

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

• Trough Plasma Concentration (Ctrough) of Simeprevir
• Time to Reach Maximum Plasma Concentration (Tmax) of Simeprevir
• Average Plasma Concentration at Steady State (Cavg,ss) of Simeprevir
• Fluctuation Index (FI) of Simeprevir
• Trough Plasma Concentration (Ctrough) of Ledipasvir
• Time to Reach Maximum Plasma Concentration (Tmax) of Ledipasvir
• Average Plasma Concentration at Steady State (Cavg,ss) of Ledipasvir
• Fluctuation Index (FI) of Ledipasvir

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the primary endpoint as a continuous measure summarized by its mean and standard deviation. A mean describes the arithmetic average of the observed values, while a standard deviation describes how dispersed individual observations are around that average. In general, means are easy to interpret in the endpoint’s original units, but they can be influenced by unusually high or low measurements. The posted standard deviations are large, so the observed participant values vary considerably around each group mean. The registry record does not report the shape of the data distribution or whether a transformation was used in the sponsor’s analysis.

What does the recalculated mean difference represent?

The recalculated mean difference is the unadjusted difference between the two posted group means. For the primary comparison, this estimate is 4290.0 ng/mL. The interval from 1821.0 to 6759.0 is the recalculated 95% confidence interval, and the listed p-value is p < 0.001. These are simple unadjusted calculations from the posted summary statistics. They do not substitute for a model-based analysis that might account for the trial’s structure, repeated measurements, or other covariates. The registry record does not provide enough detail to determine whether or how its own analysis addressed those features.

A confidence interval gives a range of values reasonably compatible with the data under the assumptions of the calculation. It does not mean that there is a 95% probability that the fixed true effect lies inside this particular interval. Rather, in general, the method is designed so that intervals produced repeatedly under its assumptions would cover the true value at the stated rate. That interpretation depends on the method’s assumptions being suitable for the data and design.

Why is the reported ratio not the same as the recalculation?

The sponsor’s reported result is a least-squares means ratio of 4.7 with a 90% confidence interval from 3.4 to 6.5. A ratio compares levels proportionally, while a mean difference compares them by subtracting one mean from another. The registry record does not identify the model, transformation, adjustment variables, or exact inferential procedure for the ratio. The posted recalculation is explicitly unadjusted and is on the original concentration scale. The two analyses answer related but not identical statistical questions, and their confidence intervals have different stated coverage levels.

In general, least-squares means are model-based means or contrasts that may be adjusted for variables included in a fitted model. Their meaning depends on the model specification. Without that specification, the reported ratio should be described as the sponsor’s posted analysis, not reverse-engineered or treated as a plain ratio of the two displayed arithmetic means. The record does not report enough information to reproduce that result.

What does a p-value say?

In general, a p-value measures how incompatible the observed data, or more extreme data, would be with a specified null hypothesis 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 recalculated p-value is unadjusted. The registry record does not state whether the sponsor’s analysis adjusted for multiple endpoints or comparisons, and the reported sponsor analysis has no p-value listed.

Unadjusted recalculations are useful as transparent checks based on displayed summary statistics, but they may not reproduce a planned analysis. For example, an analysis using repeated observations from the same participants could account for correlation between observations, while a simple independent-groups calculation would not. General statistical practice requires matching the analysis to the design and estimand. The record does not supply the primary model details needed to verify such alignment.

Why can over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. If an analysis assumes less variability than the data actually contain, standard errors can be too small and confidence intervals too narrow; if variability is modeled appropriately, uncertainty is more accurately represented. For continuous concentration outcomes, the relevant distributional assumptions and variance structure should be checked against the data and design. The registry record does not report a dispersion model, diagnostic checks, or individual-level data, so no conclusion about over-dispersion or its handling is possible.

The primary outcome is sampled at multiple times within a dosing interval and across Day 14 and Day 28, but the primary result is posted as a summary mean for each condition. In general, using a minimum selected from multiple observations can have different statistical properties from analyzing a single prespecified timepoint. The endpoint definition identifies Cmin as the minimum observed concentration, but the record does not explain exactly how the minimum was derived for each participant or how missing sampling times were handled.

The study is labeled randomized and parallel, while the primary posted contrast is labeled by regimen and day within Panel 1. In general, randomization supports unbiased comparisons when the groups being compared were assigned through the randomization process and the analysis respects that assignment. Here, the record does not specify whether the displayed Day 14 and Day 28 measurements are from the same participants, nor does it describe the randomization’s relationship to this contrast. That uncertainty limits claims about causal attribution. The posted values can be described as a difference between labeled conditions, but the registry record alone does not establish the precise causal interpretation or statistical model behind it.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 4290.0 ng/mL, with a 95% confidence interval from 1821.0 to 6759.0. This interval describes uncertainty around the unadjusted contrast, given the calculation’s assumptions. Its limits are both greater than zero, and the recalculated p-value is p < 0.001. Those features indicate that the simple unadjusted calculation distinguishes the displayed means statistically, but they do not address whether its assumptions fully reflect the study design.

The registry’s own analysis reports a least-squares means ratio of 4.7 and a 90% confidence interval from 3.4 to 6.5. The interval is on a ratio scale and has a different confidence level from the recalculated difference interval. The two intervals should not be compared as if they measured uncertainty on the same scale or arose from the same analysis. The method for the sponsor’s model-based estimate is not reported in the registry record.

Precision is affected by the amount of participant-level variation, the number of observations, and the analysis structure. The primary summary includes 20 participants in each condition, and the standard deviations are 3778.0 and 4179.0. The posted dispersion indicates substantial variation, while the confidence interval shows the resulting uncertainty in the unadjusted mean contrast. Without individual data, it is not possible to assess whether the distribution is skewed, whether there are influential observations, or how much repeated-measure correlation affects precision.

Confidence intervals quantify statistical uncertainty under a chosen method; they do not capture every source of uncertainty. In this study, the difference between regimen and assessment day, and the unreported analysis details, also affect how confidently the contrast can be attributed to the pharmacokinetic interaction of interest. The interval is therefore most directly read as precision for the recalculated numerical contrast, not as a complete measure of uncertainty about a causal interaction effect.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the study’s original design calculation. For continuous outcomes, the figures are participants per arm. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The registry record does not report the original sample-size justification or its design assumptions.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect at the assumed significance level, if the assumptions and effect were correct. The 90% power column uses a higher chance of detection under those same assumptions and therefore generally requires more participants per arm. These are design calculations for hypothetical future studies, not a description of the probability that the completed study detected an effect.

Rows based on 100% of the observed effect use the effect size estimated in this trial as the planning target. Rows based on 75% or 50% of the observed effect use smaller target effects. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm, all else held constant. The displayed values are conditional on the planning assumptions; changes in variability, allocation, analysis method, or target effect can change the sample size required.

These figures are not observed power. They do not indicate the probability that the trial’s findings are true, nor do they explain why the trial enrolled its observed number of participants. Because they are derived from the observed effect, they should be treated as illustrative rather than as a retrospective evaluation of the study’s success. The record does not report the original planning rationale.

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 = 4290.000; pooled standard deviation σ = 3983.549.
2. n = 2 × (1.96 + 0.842)² × 3983.549² / 4290.000² = 13.5, rounded up to 14 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 <- 4290                      # observed difference in means
sigma <- 3983.54898300498                     # 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(2421211)
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 = 14 (80% power), 19 (90% power)
 75% of observed effect: n per arm = 25 (80% power), 33 (90% power)
 50% of observed effect: n per arm = 55 (80% power), 73 (90% power)
power.t.test: 14.6 
Simulated power at n = 14 per arm: 0.785 (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’s own primary analysis reports a least-squares means ratio of 4.7, with a 90% confidence interval from 3.4 to 6.5. This is the sponsor’s posted analysis and should be distinguished from the unadjusted recalculation of the displayed means. The recalculation expresses an absolute mean difference of 4290.0 ng/mL and gives a 95% confidence interval from 1821.0 to 6759.0, with p < 0.001.

The sponsor’s ratio and the recalculated difference use different scales and different confidence levels. A ratio describes a relative contrast; a difference describes an absolute concentration contrast. The registry record does not report the model or method used to obtain the least-squares means ratio, and no p-value is listed for that analysis. Consequently, the sponsor result cannot be reproduced or fully compared with the simple recalculation using the information in the record.

The discrepancy flag is false, so no discrepancy between the posted sponsor estimate and the recalculation is flagged. That does not make the two statistics identical: their scales and reported confidence levels remain different. The recalculation is a transparent, unadjusted check based on the posted means and standard deviations, not a replacement for the sponsor’s own analysis. For interpretation of the trial’s planned analysis, the sponsor’s result remains the relevant posted analysis, while the recalculation provides a separate view of the summary data.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 20 outcome measures and 6 analyses. It does not report a multiplicity procedure, such as an adjustment to account for testing several outcomes or comparisons, nor does it describe a formal hierarchy for deciding which results are confirmatory. Without that information, the unadjusted p-values should be interpreted as applying to their individual comparisons rather than as controlling the chance of at least one false-positive result across all analyses. This is particularly relevant for secondary outcomes, which are numerous and may be related to one another.

The primary analysis population is defined as all participants who took at least 1 dose of simeprevir, ledipasvir, or sofosbuvir. The registry record does not report how many participants were excluded from that set, whether all enrolled participants contributed to each endpoint, or the rules for handling missing data. For several posted measures, the group counts differ; the reason for those differences is not reported in the registry record. The record does not explain whether missing concentrations were imputed, whether incomplete sampling led to exclusion, or how withdrawals were handled.

Randomization is recorded, but the randomization procedure, allocation ratio, concealment approach, and treatment of departures from assigned regimens are not reported in the registry record. Masking is listed as none. The record defines an ITT analysis set by receipt of at least one dose, but does not provide further detail about adherence to that definition for each analysis. It also does not report whether analyses were adjusted for baseline characteristics or other covariates.

The sponsor’s reported primary analysis is a least-squares means ratio, but its model specification and inferential method are not reported in the registry record. The simple recalculation uses posted summary statistics and is unadjusted. Neither the registry listing nor the recalculation supplies individual-level evidence for assessing distributional assumptions, outliers, missingness mechanisms, or within-participant correlation. These omissions limit independent evaluation of the statistical plan and the robustness of the estimates. They do not invalidate the posted numbers, but they constrain the strength and scope of conclusions that can be drawn from them.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: fibula fracture (5.0%), tibia fracture (5.0%).

The registry lists serious adverse events affecting 2 of 20 participants in the Panel 1 group and 0 of 20 participants in the Panel 2 group. These are participant counts in the posted safety groups. The record also lists fibula fracture and tibia fracture among the top serious adverse event terms, each at 5.0%. It does not establish from these counts alone whether an event was caused by a study medicine.

Serious adverse event counts are descriptive and should be read separately from the pharmacokinetic efficacy measures. With the reported group sizes, the counts provide limited information about uncommon events, and the registry record does not give a comparative statistical analysis for safety. Other adverse events are listed for 17 of 20 participants in Panel 1 and 15 of 20 in Panel 2; those counts concern the registry’s other-adverse-event category, not serious events.

Death counts are not reported in the registry record. The safety figures should not be interpreted as proving that serious harms did or did not occur beyond the events recorded in these groups. They are a registry snapshot of reported counts, not a complete assessment of causality or comparative safety.

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

The posted primary data show a higher mean simeprevir minimum plasma concentration for the Panel 1 Day 28 regimen/timepoint condition than for the Panel 1 Day 14 condition. The recalculated unadjusted mean difference is 4290.0 ng/mL, and the 95% confidence interval runs from 1821.0 to 6759.0. The sponsor’s analysis reports a least-squares means ratio of 4.7 with a 90% confidence interval from 3.4 to 6.5. These results describe measured drug concentration under the labeled conditions.

They do not by themselves show that adding ledipasvir caused the observed difference. The posted contrast changes both the regimen label and the assessment day, and the registry record does not explain whether the measurements came from the same participants or how time and repeated observations were modeled. The randomized designation for the overall study cannot, without those details, resolve the interpretation of this particular contrast.

The findings do not establish that a regimen improves hepatitis C cure rates, symptoms, quality of life, or other patient outcomes. The primary endpoint is a pharmacokinetic concentration measure, and no such clinical outcome result is included in the primary comparison. Nor do the results establish that the combination is safe or unsafe; the serious adverse event counts are descriptive and limited in size.

The most defensible interpretation is therefore narrow: the posted Panel 1 concentration summaries differ in the indicated direction, with uncertainty quantified by the reported intervals, and the sponsor also reports a relative estimate. The data are relevant to characterizing drug exposure, but incomplete design and analysis details limit attribution of the difference and the conclusions that can be extended beyond the measured pharmacokinetic outcomes.

18. Why This Trial Matters Statistically

This study illustrates why a pharmacokinetic result must be interpreted in relation to the exact comparison, not only the numerical contrast. The primary endpoint is a concentration measure, and the posted Panel 1 comparison pairs different assessment days with different regimen descriptions. Recognizing that structure prevents the numerical difference from being casually attributed to a single medicine or component of the treatment sequence.

It also demonstrates how different estimands can coexist in one registry result. The sponsor reports a least-squares means ratio, while the unadjusted recalculation reports a difference in the original concentration units. Both summarize a contrast, but they communicate different quantities and use different confidence levels. Clear distinction between relative and absolute effects is essential for readers evaluating pharmacokinetic results.

The record also shows the role and limits of confidence intervals and planning illustrations. The primary interval communicates uncertainty around the recalculated difference under its assumptions. Planning figures show how future sample sizes depend on the effect targeted and desired power; they do not describe observed power or reveal the trial’s original rationale. Keeping those concepts separate avoids retrospective claims that the trial was or was not adequately powered based on a post hoc calculation.

Finally, the study emphasizes the importance of transparent reporting. Model details, multiplicity handling, missing-data procedures, and the relationship between randomization and the displayed contrast are not reported in the registry record. Those omissions do not erase the recorded concentration data, but they affect reproducibility and causal interpretation. For biostatisticians and clinical researchers, the central lesson is to connect each estimate to its measurement scale, design context, and documented analysis before drawing broader conclusions.

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 main limitation for interpreting the primary result is that the two conditions differ in both regimen and assessment day. The registry record does not state whether the Day 14 and Day 28 observations were obtained from the same participants, or explain how the analysis handled any repeated measurements. As a result, the displayed contrast does not isolate the contribution of ledipasvir, and a simple independent-groups recalculation may not reflect the structure of the underlying data.

The sponsor’s analysis method is not described beyond the reported least-squares means ratio. Model terms, adjustment variables, transformation, variance assumptions, and handling of within-participant dependence are not reported in the registry record. The unadjusted recalculation is based on summary statistics and cannot be used to verify those model choices. Individual-level data and diagnostic information are also not reported, limiting assessment of skewness, influential observations, and the distribution of concentration values.

Missing-data rules, endpoint-specific analysis counts, adherence details, and the reason for differing counts across some summaries are not reported in the registry record. Multiplicity handling across the many outcomes and analyses is likewise not reported. The record lists 41 enrolled participants, while the primary comparison includes 20 participants per condition; the registry record does not explain the relationship between overall enrollment and those analysis counts.

The available treatment description for Panel 1 is incomplete, and the registry record does not explain how the randomization scheme relates to the primary comparison. Numerical secondary results are available for only some of the named outcomes. Safety counts are descriptive, and death counts are not reported in the registry record. These specific reporting gaps limit independent assessment of the treatment contrast, the generalizability of the exposure pattern, and the completeness of the safety account.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Investigate the Pharmacokinetic Interactions Between Simeprevir and Ledipasvir in a Treatment Regimen Consisting of Simeprevir, Sofosbuvir, and Ledipasvir in Treatment-naive Participants With Chronic Hepatitis C Virus Genotype 1 Infection — NCT02421211.
• Registry record last updated 2019-03-28; status last verified 2019-03.
• Results first posted 2017-01-05.
• 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

NCT02421211 is a completed Phase 2, randomized, open-label, parallel study sponsored by Janssen Sciences Ireland UC. It enrolled 41 treatment-naive participants with chronic hepatitis C virus genotype 1 infection. The study investigated pharmacokinetic interactions involving simeprevir, sofosbuvir, and ledipasvir in two panels.

The primary endpoint was simeprevir minimum plasma concentration. In Panel 1, the posted Day 14 mean was 2411.0 ng/mL among 20 participants, and the Day 28 mean was 6701.0 ng/mL among 20 participants. The sponsor reports a least-squares means ratio of 4.7 with a 90% confidence interval from 3.4 to 6.5; the unadjusted recalculation reports a mean difference of 4290.0 ng/mL with a 95% confidence interval from 1821.0 to 6759.0.

The contrast describes different regimen and assessment-time conditions and should not be treated as isolating a single component without further design and analysis information. Secondary pharmacokinetic measures and descriptive safety counts are also recorded, while several statistical details are not reported in the registry record.