Ledipasvir/Sofosbuvir Fixed-Dose Combination Plus Ribavirin in Participants With Chronic HCV With Advanced Liver Disease or Post-Liver Transplant: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ledipasvir/Sofosbuvir Fixed-Dose Combination Plus Ribavirin in Participants With Chronic HCV With Advanced Liver Disease or Post-Liver Transplant (NCT02010255), a randomized phase 2 study. The primary outcome is Percentage of Participants With Sustained Virologic Response (SVR) 12 Weeks After Discontinuation of Therapy (SVR12).

2. Clinical Question

The clinical question is therefore about virologic response after two durations of the same drug combination across participants with substantially different liver disease and transplant status. The randomized comparisons apply within the assigned groups, while comparisons across different clinical groups also reflect differences in the populations enrolled. The posted results should be read with those distinctions in mind, especially for groups with small numbers of participants.

3. Trial Design

This was a completed phase 2, multicenter, open-label, randomized, parallel-group study. The registry lists enrollment of 334 participants. Randomization was 1:1 within clinical groups to 12 or 24 weeks of ledipasvir/sofosbuvir plus ribavirin. Participants and study personnel were not masked, according to the registry record.

The study had two broad cohorts. Cohort A comprised participants with decompensated cirrhosis and no prior liver transplant. Its groups were distinguished by CPT class: Class B (7-9) and Class C (10-12). Cohort B comprised post-transplant participants, with or without cirrhosis. The groups included F0-F3 fibrosis, CPT Class A (5-6), CPT Class B (7-9), CPT Class C (10-12), and fibrosing cholestatic hepatitis. Each listed group had a 12-week and a 24-week regimen.

All arms used the same ledipasvir/sofosbuvir combination with ribavirin; treatment duration was the planned randomized contrast. Ribavirin starting dose and adjustment instructions varied among groups, as described in the arm descriptions. The registry record does not report a separate untreated or active-drug comparator.

The primary outcome was assessed after treatment, at posttreatment Week 12. The analysis population was the full analysis set: randomized participants who received at least one dose of study drug, with Cohort A participants who received a liver transplant before the lower bound of the posttreatment Week 12 visit excluded from that analysis. The registry record does not report a detailed protocol for handling other missing outcome data, nor does it report the original sample-size justification or the planned statistical analysis methods. Results therefore need to be interpreted as posted group-specific outcomes and unadjusted recalculations, rather than as a complete account of the sponsor's prespecified analysis.

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: * Cohort A: decompensated cirrhosis \[advanced liver disease\], no prior liver transplant; * Cohort B: post-liver transplant, with or without cirrhosis; * Group assignment within cohorts was based on severity of liver impairment at screening \[or presence of disease for FCH groups\]; * Randomization was 1:1 within groups to 12 or 24 weeks of treatment.

Only the first 6 of 14 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: participants who were randomized and received at least one dose of study drug. Participants in Cohort A who received a liver transplant prior to the lower bound of the Posttreatment Week 12 visit were not included in the analysis.

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.

Population: Safety Analysis Set: participants who were enrolled and received at least one dose of study drug

Only the first 6 of 15 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Sustained Virologic Response (SVR) 12 Weeks After Discontinuation of Therapy (SVR12), measured over Posttreatment Week 12.

The primary endpoint was the percentage of participants with sustained virologic response 12 weeks after discontinuing therapy, called SVR12. The registry defines response as HCV RNA below the lower limit of quantitation, specified as 15 IU/mL, at 12 weeks after treatment stopped.

This outcome captures whether viral RNA remains below the stated measurement threshold at a follow-up point after the treatment course, rather than only measuring viral RNA during treatment. It is useful for comparing post-treatment virologic outcomes because the assessment occurs after participants have stopped taking study medication. It is a binary outcome at the participant level: each person either meets the stated response definition or does not, and the reported endpoint is the percentage meeting it.

Interpretation depends on the analysis population and the timing definition. The registry specifies the full analysis set as randomized participants who received at least one dose, with the stated exclusion for certain Cohort A participants who received a transplant before the posttreatment Week 12 visit. The record does not describe how all other absent or unevaluable Week 12 results were handled. The percentages therefore need to be understood in the context of that defined population, not assumed to represent every randomized participant.

SVR12 is the primary endpoint; other posted measures include response at different follow-up times, early HCV RNA thresholds, and virologic failure. Those outcomes provide related but distinct information. A response at an earlier time point is not the same endpoint as SVR12, and the registry record does not make the secondary measures substitutes for the primary outcome.

7. Results Posted in the Registry

• Cohort A, Group 1 (24 wk): CPT Class B (7-9): 96.0% (24/25) versus 84.6% (22/26) on control; risk difference 11.4 percentage points (95% CI -4.5 to 27.2), risk ratio 1.13 (0.95–1.36); unadjusted two-proportion z-test p = 0.172.
• Cohort A, Group 2 (12 wk): CPT Class C (10-12): 81.0% (17/21) versus 84.6% (22/26) on control; risk difference -3.7 percentage points (95% CI -25.4 to 18.1), risk ratio 0.96 (0.73–1.25); unadjusted two-proportion z-test p = 0.740.
• Cohort A, Group 2 (24 wk): CPT Class C (10-12): 76.0% (19/25) versus 84.6% (22/26) on control; risk difference -8.6 percentage points (95% CI -30.4 to 13.1), risk ratio 0.90 (0.68–1.18); unadjusted two-proportion z-test p = 0.439.
• Cohort B, Group 3 (12 wk): F0-F3 Fibrosis: 94.2% (49/52) versus 84.6% (22/26) on control; risk difference 9.6 percentage points (95% CI -5.6 to 24.9), risk ratio 1.11 (0.93–1.33); unadjusted two-proportion z-test p = 0.161.

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.

Percentage of Participants With Virologic Failure

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cohort A, Group 1 (24 wk): CPT Class B (7-9): 4.0% (1/25) versus 15.4% (4/26) on control; risk difference -11.4 percentage points (95% CI -27.2 to 4.5), risk ratio 0.26 (0.03–2.17); unadjusted two-proportion z-test p = 0.172.
  • Cohort A, Group 2 (12 wk): CPT Class C (10-12): 9.5% (2/21) versus 15.4% (4/26) on control; risk difference -5.9 percentage points (95% CI -24.6 to 12.8), risk ratio 0.62 (0.13–3.06); unadjusted two-proportion z-test p = 0.549.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort A, Group 1 (24 wk): CPT Class B (7-9) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort A, Group 2 (12 wk): CPT Class C (10-12) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With HCV RNA < LLOQ at Week 1

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cohort A, Group 1 (24 wk): CPT Class B (7-9): 3.7% (1/27) versus 3.8% (1/26) on control; risk difference -0.1 percentage points (95% CI -10.4 to 10.1), risk ratio 0.96 (0.06–14.60); unadjusted two-proportion z-test p = 0.978.
  • Cohort A, Group 2 (12 wk): CPT Class C (10-12): 12.0% (3/25) versus 3.8% (1/26) on control; risk difference 8.2 percentage points (95% CI -6.6 to 22.9), risk ratio 3.12 (0.35–28.03); unadjusted two-proportion z-test p = 0.279.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort A, Group 1 (24 wk): CPT Class B (7-9) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort A, Group 2 (12 wk): CPT Class C (10-12) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With HCV RNA < LLOQ at Week 2

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cohort A, Group 1 (24 wk): CPT Class B (7-9): 37.0% (10/27) versus 26.9% (7/26) on control; risk difference 10.1 percentage points (95% CI -14.8 to 35.1), risk ratio 1.38 (0.62–3.07); unadjusted two-proportion z-test p = 0.430.
  • Cohort A, Group 2 (12 wk): CPT Class C (10-12): 40.0% (10/25) versus 26.9% (7/26) on control; risk difference 13.1 percentage points (95% CI -12.6 to 38.8), risk ratio 1.49 (0.67–3.29); unadjusted two-proportion z-test p = 0.322.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort A, Group 1 (24 wk): CPT Class B (7-9) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cohort A, Group 2 (12 wk): CPT Class C (10-12) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary SVR12 assessment in two broad ways: they track response at other follow-up times and describe virologic measures during or after therapy. The registry lists SVR at post-treatment Weeks 2, 4, 8, and 24, virologic failure, post-transplant virologic response at post-transplant Week 12, and HCV RNA below the lower limit of quantitation at early treatment weeks. These outcomes provide context about timing and durability, but each answers a distinct question.

The posted secondary results show that response percentages and virologic failure percentages vary across clinical groups, as do early HCV RNA results. They should be considered alongside the primary endpoint rather than as interchangeable evidence. An early viral RNA threshold is not the same as sustained response after treatment; a virologic failure measure is also distinct from the primary response definition. A pattern in one secondary measure does not automatically confirm or contradict the SVR12 result.

The record lists 25 outcome measures and reports 23 posted secondary outcomes. Many possible comparisons arise from assessing several outcomes across groups and follow-up times. Unless the analysis plan defines how to control the chance of false-positive findings across those comparisons, an isolated unadjusted p-value deserves less weight than a result from a prespecified, multiplicity-controlled analysis. The registry record does not report a multiplicity adjustment strategy or sponsor analyses for the posted recalculations.

In general, secondary endpoints are valuable for describing the broader outcome pattern and for generating questions for further study. They are less persuasive as stand-alone confirmatory evidence when numerous outcomes and subgroups are examined without a reported hierarchy or adjustment. The appropriate reading is therefore descriptive: secondary results can help characterize the timing and pattern of virologic outcomes, but the primary endpoint remains the designated main outcome, and the registry record does not establish a formal confirmatory role for the secondary measures.

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

• Percentage of Participants With SVR 2 Weeks After Discontinuation of Therapy (SVR2)
• Percentage of Participants With SVR 4 Weeks After Discontinuation of Therapy (SVR4)
• Percentage of Participants With SVR 8 Weeks After Discontinuation of Therapy (SVR8)
• Percentage of Participants With SVR 24 Weeks After Discontinuation of Therapy (SVR24)
• Percentage of Participants With Virologic Failure
• Percentage of Participants With Posttransplant Virologic Response (pTVR) at Posttransplant Week 12
• Percentage of Participants With HCV RNA < LLOQ at Week 1
• Percentage of Participants With HCV RNA < LLOQ at Week 2

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is binary: a participant either met the SVR12 definition or did not. For a binary endpoint, a percentage is an intuitive summary of the observed proportion meeting the definition. It does not, on its own, show how uncertain that proportion is. Uncertainty depends in part on the number of observations and on how many participants meet the outcome, so equal-looking percentages can carry very different precision in groups of different sizes.

What does the risk difference describe?

The posted recalculations use risk difference. This expresses the difference between two observed proportions, preserving the outcome's absolute scale. A risk difference of zero corresponds to equal observed proportions; a positive or negative value indicates which of the two proportions is larger according to the subtraction order used in the comparison. In this record, comparisons are oriented against the designated Cohort A, Group 1 (12 weeks) reference. The numerical estimate is accompanied by a confidence interval, which represents a range of values compatible with the observed data under the method's assumptions.

Risk difference is distinct from a risk ratio or odds ratio. These measures express a contrast on different scales and can appear quite different, especially when event percentages are near the boundaries. The posted recalculations include risk ratios and odds ratios for some comparisons, but they are not substitutes for interpreting the primary percentages. The estimates are unadjusted and are based on the posted summary counts.

How should the p-values be read?

The p-values in the recalculated comparisons are unadjusted. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. A small p-value does not establish that a difference is meaningful, and a larger p-value does not demonstrate that two groups are equivalent. Confidence intervals are useful alongside p-values because they show the range and direction of estimates compatible with the data.

The registry record does not report a sponsor analysis for these comparisons. The displayed recalculations should therefore be treated as simple, unadjusted comparisons from posted summary statistics, not as a replacement for a prespecified trial analysis. The record does not report whether the sponsor used a model accounting for clinical strata, baseline factors, or the design's group-specific randomization.

Why do group sizes and clinical strata matter?

Randomization was 1:1 within groups, and each group was defined by disease severity or transplant-related status. This means the direct randomized question is the comparison of the two durations within a given group. Comparing a Cohort B group with the Cohort A reference changes both the duration or group and the underlying clinical population. Such contrasts are descriptive, not a clean randomized comparison of duration across populations.

Some groups contain few participants. With sparse binary data, one participant's outcome can change the observed proportion substantially. Estimates can consequently be unstable, and confidence intervals can be wide. A result of 100.0 in a small group does not establish that the underlying response probability is exactly 100.0; it describes the observed participants. Similarly, a low percentage in a small group should be read cautiously rather than treated as a precise estimate for a broader population.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimate under the statistical method used. For a risk difference, an interval containing zero is compatible with no difference as well as with effects in either direction within the interval. An interval that excludes zero indicates that the corresponding unadjusted interval calculation does not include zero, but it does not address multiplicity, bias, or whether the effect is important. A narrow interval indicates greater precision than a wide one, though both remain dependent on the quality and assumptions of the data and method.

General statistical context: interval estimates quantify sampling uncertainty, not every possible source of uncertainty. They do not repair problems caused by missing outcome data, differences between groups, or an analysis plan that is not reported. In this study, the posted comparisons have varying group sizes, and the confidence intervals should be considered together with the group definitions and the primary analysis population.

What is not established by the record?

The registry record does not report the original sample-size rationale, detailed missing-data methods, the sponsor's full analysis plan, interim analyses, or a multiplicity strategy. These omissions matter because the study has several clinical groups, durations, endpoints, and follow-up times. Without a posted prespecified analysis framework, the recalculated comparisons should be viewed as exploratory descriptions of selected contrasts rather than a complete set of confirmatory tests. The statistical interpretation is consequently limited to what the posted data and definitions support.

11. Confidence Intervals and Precision

Precision differs markedly across the groups. Arm sizes range from groups with only a few participants to groups with several dozen, and the observed percentages should be interpreted in that context. A percentage from a small group can change sharply when the outcome of one participant changes; the same percentage in a larger group is generally less sensitive to a single observation. The registry does not report confidence intervals for the individual arm percentages.

The recalculated risk-difference intervals also show uncertainty in the comparisons. For the 24-week Cohort A CPT Class B group versus the reference, the interval extends from -0.045 to 0.272. For the 12-week Cohort A CPT Class C group versus the reference, it extends from -0.254 to 0.181. Such intervals include values on both sides of zero, so the observed data do not precisely distinguish the direction of those contrasts under the unadjusted calculation.

Some intervals are more limited in direction: the 24-week F0-F3 comparison has a risk-difference interval from 0.015 to 0.292, while the 24-week Cohort B CPT Class B comparison has an interval from 0.015 to 0.292. These are recalculated estimates against the Cohort A reference, not adjusted within-stratum duration effects. An interval excluding zero does not by itself resolve the study's multiple-comparison concerns or establish that a contrast is clinically important.

Confidence intervals are not guarantees about the true value; in general, they describe uncertainty under the statistical method and assumptions used. Their interpretation is especially cautious where group sizes are small, event patterns are sparse, or comparisons cross distinct clinical strata. The registry record does not report sponsor confidence intervals or a complete prespecified inferential analysis, so the posted recalculated intervals should be understood as descriptive statistical summaries rather than definitive trial-wide conclusions.

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 display is a planning illustration based on the observed effect in a comparison, not the trial's original design calculation. For these binary outcomes, the figures are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planned effect is set at the stated fraction of the observed effect. The registry record does not report the original sample-size justification or its assumptions.

The 80% power column gives the illustrative number of participants per arm needed, under those assumptions, to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding number per arm for a 90% chance. These are design-planning probabilities under a model, not the probability that the trial's finding is correct.

Rows for 100% of the observed effect use the full observed contrast as the assumed target. Rows for 75% and 50% use smaller effects. Detecting smaller effects generally requires more participants, so the listed planning numbers increase as the assumed fraction of the observed effect decreases. Some illustrations can become very large when the observed contrast is close to zero; this reflects the difficulty of distinguishing a very small difference from no difference under the stated framework.

These figures are not observed power. They are not a post hoc measure of whether the completed trial succeeded, and they do not establish that the original study was adequately or inadequately sized. They also do not replace a trial-specific design calculation using its prespecified endpoint, allocation structure, assumptions, and analysis plan. The sample-size curve should be read as a visual counterpart to the same planning assumptions: as the target effect becomes smaller, the required participants per arm rise. The illustrations do not account for details absent from the registry record, including any original stratified design rationale or planned adjustment.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.846; treatment proportion p₁ = 0.960; average p̄ = 0.903.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4184 = 0.8200.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4106 = 0.3456.
4. n = (0.8200 + 0.3456)² / (0.1138)² = 104.8, rounded up to 105 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.846153846153846                          # control proportion
p1 <- 0.96                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2010255)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 105 (80% power), 140 (90% power)
 75% of observed effect: n per arm = 212 (80% power), 283 (90% power)
 50% of observed effect: n per arm = 531 (80% power), 710 (90% power)
power.prop.test: 104.8 
Simulated power at n = 105 per arm: 0.832 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The study reports a primary endpoint and numerous secondary outcome measures, with results across multiple clinical groups and two treatment durations. That creates many possible comparisons. When many statistical tests are considered, the chance of seeing at least one apparently unusual result by chance can increase. A prespecified multiplicity strategy may define which comparisons are confirmatory and how error rates are handled. The registry record does not report such a strategy for the posted results.

The pairwise p-values and confidence intervals presented in the recalculated comparisons are unadjusted. They should not be interpreted as if they came from a single prespecified test or as if their nominal uncertainty automatically applied across all possible endpoints and groups. The record lists no reported analyses, and the sponsor's complete inferential analysis is not available in the registry record. The posted recalculations are not a substitute for that analysis.

Missing outcome data also affect interpretation. The primary population is defined as randomized participants who received at least one dose, with Cohort A participants receiving a liver transplant before the lower bound of the posttreatment Week 12 visit excluded. The registry record does not report the detailed handling of other missing or unevaluable SVR12 results, such as whether they were counted as nonresponse, excluded, or handled through another procedure. The reported percentages should not be assumed to follow any particular missing-data convention beyond the population definition expressly stated.

Randomization was within groups, so analysis needs to respect the clinical group structure when estimating duration effects. The record does not report whether the sponsor's analysis included stratification or adjustment, nor does it report the full statistical model. The recalculated reference comparisons are unadjusted and should not be mistaken for a single pooled or adjusted treatment effect.

Finally, the registry record does not report interim analyses, stopping rules, or the original sample-size justification. Their absence from the record is not evidence that such procedures were or were not used; it means they are not reported in the registry record. These gaps limit assessment of the intended statistical hierarchy, missing-data assumptions, and full analysis population. Accordingly, numerical findings should be read as posted outcome descriptions and simple unadjusted comparisons, with appropriate caution about multiplicity and analysis choices.

15. 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: herpes zoster (50.0%), device dislocation (33.3%), haemophilus infection (33.3%), pneumonia (33.3%), sepsis (33.3%).

Serious adverse event figures are reported by treatment group as the number affected among participants at risk. They are counts, not percentages, and should be read separately for each group. For example, the Cohort A, Group 1 12-week group had 3 serious adverse events among 28 at risk, while its 24-week group had 6 among 28 at risk. In Cohort B, Group 3, the corresponding counts were 9 among 52 for 12 weeks and 5 among 49 for 24 weeks. Other groups have their own counts, including sparse groups where small changes in counts would be consequential.

These entries do not establish that duration caused any difference. The registry record does not provide adjusted safety comparisons or uncertainty intervals for these counts, and safety follow-up and outcome definitions should not be assumed to be identical beyond what is reported. The figures describe participants affected, not the total number of serious events; event counts per participant are not reported.

The record also lists serious adverse event terms and their percentages, including herpes zoster, device dislocation, Haemophilus infection, pneumonia, sepsis, and post procedural haemorrhage. The denominator for those listed percentages is not reported in the registry record, so they should not be treated as population risks. Death counts are not reported in the registry record. These summaries are descriptive safety information, not a basis for attributing an event to treatment.

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

The results describe SVR12 percentages among the defined analysis population in groups receiving ledipasvir/sofosbuvir plus ribavirin for 12 or 24 weeks. Several groups had high observed response percentages, while some advanced-disease groups had lower percentages. The results also show that the numerical pattern is not consistent across all clinical categories. Differences in percentages are observations in these study groups, not proof that a duration caused a particular response rate.

The randomization makes within-group duration comparisons the most relevant contrasts for assessing duration, because participants were assigned within groups. However, the registry record does not report a complete sponsor analysis or adjustment strategy, and the posted recalculations compare each selected group with the Cohort A CPT Class B 12-week reference. Comparisons across cohorts or disease-severity groups also involve different participant populations and should not be attributed to duration alone.

These data do not establish that the combination works or does not work, and they do not provide a treatment recommendation. They are not a comparison with no treatment or with another drug regimen. They also do not establish that one duration is superior across every clinical group. Interpretation is limited by variable group sizes, especially in the smallest post-transplant groups, the uncertainty around estimates, the number of outcomes and possible comparisons, and the absence of a reported comprehensive statistical analysis.

The study's outcome definition is specific: HCV RNA below the stated quantitation limit at posttreatment Week 12. It does not answer every question about longer-term outcomes, safety, or people outside the enrolled clinical categories. Secondary outcomes add context but have their own definitions and timing. The registry record does not report the original sample-size rationale or complete missing-data methods, so it cannot establish how the study was designed to resolve small differences or how all unevaluable outcomes were handled.

The sound conclusion is limited to description: the posted percentages vary by group and duration, and several comparisons are imprecise. Any broader claim requires a prespecified analysis that respects randomization within groups, addresses multiple testing and missing outcomes, and gives appropriate weight to the small samples. Those details are not reported in the registry record.

17. Why This Trial Matters Statistically

This study is statistically notable for its combination of within-group randomization and clinically distinct strata. The design recognizes that participants with decompensated cirrhosis, post-transplant status, different CPT classes, fibrosis stages, or FCH are not one homogeneous population. Randomizing duration within these groups supports a more focused duration comparison than would a simple contrast across all participants.

At the same time, that structure makes a single overall summary difficult to interpret. The group sizes vary, and some groups are very small. A high observed percentage in a sparse group may appear decisive while remaining imprecise, whereas a more moderate estimate from a larger group can be more stable. The precision information is therefore central, not secondary, to reading the response percentages.

The trial also illustrates the difference between a registry outcome listing and a complete statistical report. A defined primary endpoint is available, along with group results and recalculated comparisons, but the registry record does not report the sponsor's full analysis, multiplicity plan, missing-data procedures, interim analysis details, or original sample-size justification. Those omissions constrain confirmatory interpretation and make it important to distinguish descriptive outcomes from inferential claims.

Finally, the study asks a practical statistical question about treatment duration across several clinical contexts, but the evidence cannot be condensed into one universal duration effect from the posted summaries. The most defensible reading follows the randomized strata, examines uncertainty, and avoids treating cross-group contrasts as randomized comparisons. This is a useful example of how design structure, sparse data, and incomplete reporting shape what can be concluded from clinical trial results.

18. Limitations

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

The principal trial-specific limitation is the uneven size of the clinical groups. Several groups have only a few participants per arm, particularly the post-transplant CPT Class C and FCH groups. Their percentages can be highly sensitive to individual outcomes, and estimates should not be generalized as precise values for broader populations. Even larger groups remain limited in size for detailed subgroup comparisons.

The study is open-label, so participants and study personnel knew the assigned duration. The primary endpoint is based on a laboratory threshold, but the registry record does not report whether outcome ascertainment or other study procedures were protected from potential knowledge-of-assignment effects. The registry record also does not report the original sample-size justification or whether the study was intended to make definitive comparisons within each group.

All arms received the same drug combination, and the listed randomized contrast is duration. There is no untreated or different-regimen comparator in the registry record. Cross-cohort contrasts therefore cannot isolate a treatment effect and are affected by differences in disease severity and transplant status. The posted comparison calculations use one Cohort A group as a reference, rather than presenting a comprehensive adjusted within-stratum analysis.

The record does not report the detailed handling of missing or unevaluable primary outcomes beyond the stated full analysis set definition, nor does it report a multiplicity strategy for the many outcomes and groups. The posted p-values are unadjusted, and a full sponsor analysis is not reported in the registry record. Safety counts are descriptive; death counts are not reported in the registry record, and the denominators for listed serious adverse event terms are not reported. These limitations restrict precision, comparison, and generalization of the posted findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Ledipasvir/Sofosbuvir Fixed-Dose Combination Plus Ribavirin in Participants With Chronic HCV With Advanced Liver Disease or Post-Liver Transplant — NCT02010255.
• Registry record last updated 2018-11-19; status last verified 2016-05.
• Results first posted 2016-06-20.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT02010255 is a completed, randomized, open-label, parallel-group phase 2 study of ledipasvir/sofosbuvir plus ribavirin in participants with chronic genotype 1 or 4 HCV and advanced liver disease or post-liver transplant status. Enrollment was 334. Participants were randomized within clinical groups to 12 or 24 weeks of treatment.

The primary outcome was the percentage with SVR12, defined as HCV RNA below the lower limit of quantitation 12 weeks after treatment discontinuation. The registry reports results across Cohort A and Cohort B groups, with response percentages varying by clinical category and duration. Secondary outcomes include other response time points, virologic failure, and early HCV RNA measures.

Recalculated comparisons are unadjusted and use Cohort A, Group 1 (12 weeks) as the reference. The registry record does not report a complete sponsor analysis, multiplicity plan, detailed handling of missing outcomes, or original sample-size rationale. Small groups and varying precision warrant caution, particularly when interpreting cross-group contrasts or the smallest post-transplant categories.