Sofosbuvir/Velpatasvir Fixed-Dose Combination in Adults With Chronic HCV Infection and Child-Pugh Class B Cirrhosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Sofosbuvir/Velpatasvir Fixed-Dose Combination in Adults With Chronic HCV Infection and Child-Pugh Class B Cirrhosis (NCT02201901), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response (SVR) 12 Weeks After Discontinuation of Therapy (SVR12).

2. Clinical Question

The study also set out to evaluate safety and tolerability. Its randomized, parallel-group structure allows outcome percentages to be compared across the assigned regimens, while the open-label design means masking was not used. The primary endpoint concerns a laboratory measure at a specified post-treatment time; it does not by itself describe changes in liver status, symptoms, or every aspect of safety.

The registry describes three treatment groups: sofosbuvir/velpatasvir for 12 weeks, the same combination with ribavirin for 12 weeks, and sofosbuvir/velpatasvir for 24 weeks. The posted comparisons therefore address two distinct regimen contrasts against the 12-week sofosbuvir/velpatasvir group. The results should be read as evidence about those particular comparisons in the enrolled study population, rather than as a universal ranking of treatment approaches.

3. Trial Design

This was a phase 3, randomized, multicenter, open-label study with a parallel-group model. The registry lists enrollment as 268 and describes adults with chronic HCV infection and Child-Pugh class B cirrhosis. The study status is completed. The record gives a start date of 2014-07 and a primary completion date of 2015-08.

Participants were assigned to one of three regimens: sofosbuvir/velpatasvir fixed-dose combination for 12 weeks; sofosbuvir/velpatasvir plus ribavirin for 12 weeks; or sofosbuvir/velpatasvir for 24 weeks. The posted primary outcome group sizes are 90.0, 87.0, and 90.0, respectively. These are the denominators reported for the outcome results, and they should not be assumed to describe every analysis population or every safety assessment.

Randomization supports comparisons between assigned groups by reducing the risk that baseline characteristics determine treatment assignment. It does not guarantee that every possible difference between groups is eliminated, especially in a study of this size. Because the study was open-label, participants and study personnel were not masked to assigned treatment, according to the registry’s masking information. The registry record does not report further detail about allocation concealment or procedures used to reduce assessment bias.

The stated primary objectives were to evaluate efficacy, safety, and tolerability for the listed regimens. The principal efficacy measure was SVR12, assessed at posttreatment week 12. Other listed outcomes cover SVR4 and SVR24, HCV RNA measurements during treatment, virologic failure, and changes in MELD and Child-Pugh-Turcotte scores through posttreatment week 24. The registry record does not report the original sample-size justification, the full statistical plan, or whether interim analyses were planned.

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: 438 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS): participants who were randomized into the study and received at least 1 dose of study drug.

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 randomized into the study and received at least 1 dose of study drug.

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 is the percentage of participants with sustained virologic response 12 weeks after discontinuing study treatment. SVR12 is defined in the registry as HCV RNA below the lower limit of quantitation 12 weeks after the last dose of study drug. The endpoint is evaluated at posttreatment week 12, and the stated analysis population is the Full Analysis Set: participants randomized into the study who received at least 1 dose of study drug.

This is a binary outcome at the participant level: each participant either meets the SVR12 definition or does not. The group result expresses the number meeting the definition as a percentage of the analysis group. A virologic response at a post-treatment time point is used to describe whether the measured virus remains below the assay’s quantitation threshold after therapy has ended. It is distinct from an HCV RNA measurement taken while treatment is ongoing.

The registry reports a 95% confidence interval for each group’s percentage. That interval communicates uncertainty around the estimated group proportion; it is not a range containing a known percentage of individual participants. SVR12 is a defined virologic outcome, not a complete measure of health, liver function, safety, or long-term clinical course. Those questions require other outcomes and follow-up information. Results for each regimen therefore address the primary endpoint’s specific definition and timing, rather than every objective of the study.

7. Results Posted in the Registry

• SOF/VEL+RBV 12 Weeks (Group 2): 94.3% (82/87) versus 83.3% (75/90) on control; risk difference 10.9 percentage points (95% CI 1.8 to 20.0), risk ratio 1.13 (1.02–1.26); unadjusted two-proportion z-test p = 0.022.
• SOF/VEL 24 Weeks (Group 3): 87.8% (79/90) versus 83.3% (75/90) on control; risk difference 4.4 percentage points (95% CI -5.8 to 14.7), risk ratio 1.05 (0.93–1.19); unadjusted two-proportion z-test p = 0.396.

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:
  • SOF/VEL+RBV 12 Weeks (Group 2): 3.4% (3/87) versus 12.2% (11/90) on control; risk difference -8.8 percentage points (95% CI -16.6 to -1.0), risk ratio 0.28 (0.08–0.98); unadjusted two-proportion z-test p = 0.031.
  • SOF/VEL 24 Weeks (Group 3): 8.9% (8/90) versus 12.2% (11/90) on control; risk difference -3.3 percentage points (95% CI -12.3 to 5.6), risk ratio 0.73 (0.31–1.72); unadjusted two-proportion z-test p = 0.467.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for SOF/VEL+RBV 12 Weeks (Group 2) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SOF/VEL 24 Weeks (Group 3) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome domains extend beyond SVR12. The registry lists SVR4 and SVR24, HCV RNA status and change during treatment, virologic failure, and changes in MELD and Child-Pugh-Turcotte scores through posttreatment week 24. The posted secondary results include virologic failure; numerical results for the other listed outcome domains are not reported in the registry record.

For the secondary virologic-failure outcome, the broad ordering of the groups is directionally consistent with the SVR12 pattern: the group with the higher observed SVR12 percentage also has the lower observed virologic-failure percentage, while the 24-week group lies between the two 12-week groups. This qualitative correspondence is coherent because the endpoints describe related aspects of virologic outcome, but they are not interchangeable. They have different definitions and follow-up framing, and one result does not independently confirm another.

The recalculated pairwise comparisons for the secondary outcome are unadjusted. The registry record does not report a multiplicity strategy covering the primary and secondary outcomes or the several comparisons. When many outcomes and contrasts are examined, chance alone can produce apparently notable findings. Unadjusted secondary results should therefore carry less weight than a prespecified primary result and should generally be treated as supportive or exploratory unless a planned testing strategy is documented.

Secondary outcome results can help describe the breadth and timing of response, treatment failure, and changes in liver-related measures. However, the registry record does not report complete numeric findings for every listed secondary domain, and it does not supply the analysis details needed to assess all of them. Conclusions about those outcomes should remain limited to what is actually reported rather than inferred from the primary endpoint or from the direction of a related measure.

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

• Percentage of Participants With Sustained Virologic Response 4 and 24 Weeks After Discontinuation of Therapy (SVR4 and SVR24)
• Percentage of Participants With HCV RNA < LLOQ at Weeks 1, 2, 4, 6, 8, 10, 12, 16, 20, and 24
• Change From Baseline in HCV RNA at Weeks 1, 2, 4, 6, 8, 10, 12, 16, 20, and 24
• Percentage of Participants With Virologic Failure
• Percentage of Participants With a Decrease, No Change, or Increase Between Baseline and Posttreatment Week 24 in MELD Score
• Percentage of Participants With a Decrease, No Change, or Increase Between Baseline and Posttreatment Week 24 in Child-Pugh-Turcotte (CPT) Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: participants either satisfy the SVR12 definition or do not. For each regimen, the registry reports the percentage meeting that definition and a 95% confidence interval. A confidence interval conveys the statistical uncertainty around an estimated percentage under the assumptions of its calculation. Wider intervals generally indicate less precision, and narrower intervals generally indicate more precision. The interval is not a statement that a fixed share of individual outcomes lies inside its bounds.

What does a risk difference express?

A risk difference subtracts one group’s event proportion from another group’s event proportion. Here the recalculated contrasts use the 12-week sofosbuvir/velpatasvir group as the reference. A positive SVR12 risk difference means the estimated percentage meeting the response definition is higher in the comparison group; a negative difference would mean it is lower. The recalculated estimate for the ribavirin comparison is 0.109, with a 95% confidence interval from 0.018 to 0.200. For the 24-week comparison, it is 0.044, with a 95% confidence interval from -0.058 to 0.147. These calculations are unadjusted and use the posted group summaries.

How should a p-value be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the statistical test and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an estimated difference. The recalculated unadjusted p-values are 0.022 for the ribavirin comparison and 0.396 for the 24-week comparison. They should be interpreted alongside the estimates and confidence intervals, not in isolation. The registry’s own reported analyses list a binomial test for each group, with p < 0.001; the registry record does not give the associated parameter estimate or confidence interval in those analysis entries.

Why can estimates differ across analyses?

Statistical results can depend on the chosen population, outcome coding, test, model, and handling of incomplete observations. Recalculation from summary counts is a simple unadjusted analysis and may not reproduce a sponsor’s prespecified analysis. The registry record flags a discrepancy. In that situation, the sponsor’s own analysis takes precedence; the recalculated results are useful as a transparent, separate description of the posted summaries, not as a replacement for the sponsor’s result.

General statistical context: a binomial test evaluates a binary outcome against a specified probability under the test’s assumptions. The registry identifies binomial tests but does not report the tested parameter or further details, so the purpose of those tests cannot be inferred from the method label alone. Likewise, the record does not report whether the primary analysis adjusted for baseline factors, how missing outcome data were treated, or whether a particular confidence-interval method was used.

What does randomization contribute?

In general, random allocation is intended to make treatment groups comparable on average with respect to factors that could influence outcomes. It supports interpretation of between-group contrasts, but does not remove uncertainty from a finite study or automatically correct missing data, outcome-assessment issues, or selective reporting. Open-label assignment also means that participants and study personnel knew the assigned regimen. The registry record does not describe additional safeguards or the extent to which endpoint assessment was independent of treatment knowledge.

General statistical context: when an outcome is binary, uncertainty in a percentage depends on both the observed proportion and the number of observations contributing to it. Small groups or uncommon outcomes may yield imprecise estimates. For comparisons, the confidence interval is especially useful because it shows the range of differences reasonably compatible with the data under the analysis method. It also makes clear when a comparison remains uncertain, rather than reducing interpretation to whether a p-value crosses a threshold.

Why does multiplicity matter?

Testing several contrasts or outcomes creates more opportunities for an apparently notable result to arise by chance. Methods that control multiplicity can address this issue, but the registry record does not report a multiplicity adjustment or hierarchy among the listed endpoints. The recalculated p-values are explicitly unadjusted. General statistical context: an unadjusted p-value answers a single-test question under its assumptions; it does not account for the broader set of tests unless an adjustment or testing strategy is applied. The number of planned tests, their relationship, and any prespecified decision rules are not reported in the registry record.

Overall, the posted arm percentages, confidence intervals, and recalculated contrasts answer related but distinct questions. Arm estimates describe the observed proportion within each regimen group. Risk differences describe the estimated separation between two groups. Confidence intervals communicate precision, and p-values summarize compatibility with a null comparison. None of these measures on its own establishes causality beyond the trial’s design, clinical importance, or applicability beyond the studied population.

11. Confidence Intervals and Precision

The group-level 95% confidence intervals give a sense of precision for the estimated SVR12 percentages. The interval for 12-week sofosbuvir/velpatasvir is 74.0% to 90.4%; for 12-week sofosbuvir/velpatasvir plus ribavirin it is 87.1% to 98.1%; and for 24-week sofosbuvir/velpatasvir it is 79.2% to 93.7%. Each interval spans a range of plausible values for its group percentage under the method used. The registry record does not identify that method in detail.

For the recalculated between-group contrasts, precision is expressed on the risk-difference scale. The interval for the ribavirin comparison is 0.018 to 0.200. The interval for the 24-week comparison is -0.058 to 0.147. The first interval does not include zero, whereas the second does. This is consistent with the corresponding unadjusted p-values, but does not resolve the limitations of an unadjusted analysis or the discrepancy with the sponsor’s analysis.

Confidence intervals for separate groups should not be used as a stand-alone test of the difference between groups. The uncertainty for a contrast is captured more directly by the confidence interval for that contrast. Overlap between group-level intervals is not itself a formal test of equality, and absence of overlap is not a substitute for the reported comparison method.

All intervals remain uncertain estimates from the study groups, not guarantees about the true response rate or future participants. Their width reflects the amount of information available and the observed outcome pattern. The registry record does not report a precision target or a prespecified minimum important difference. Statistical precision therefore cannot by itself establish whether a difference is clinically meaningful.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations translate observed differences into hypothetical group sizes under stated assumptions. For these binary outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect as the effect to detect. The sample-size figures are planning illustrations based on observed effects, not the study’s original design justification.

The 80% power column describes the number of participants per arm that would, under those assumptions, give an 80% chance of detecting the specified effect if that effect were real. The 90% power column describes the corresponding number per arm for a 90% chance. These are hypothetical design calculations: they do not report how much power the completed study had, and they are not a measure of whether the observed results are reliable.

Each planning scenario is anchored to an observed contrast and then considers detecting the full observed effect or a stated fraction of it. A smaller effect is harder to distinguish from random variation, so it requires more participants under the same assumptions. The resulting figures can become very large when the observed contrast is modest. That does not mean the trial enrolled too few or too many participants by itself; interpretation also depends on the original design goals, which are not reported in the registry record.

The registry record does not report the original sample-size assumptions, target effect, or planned power for the trial. The illustrations therefore should be read as conditional planning examples, not as evidence about the design decisions made for this completed study.

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 = 0.833; treatment proportion p₁ = 0.943; average p̄ = 0.888.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4461 = 0.8744.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4394 = 0.3698.
4. n = (0.8744 + 0.3698)² / (0.1092)² = 129.8, rounded up to 130 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 <- 0.833333333333333                          # control proportion
p1 <- 0.942528735632184                          # 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(2201901)
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 = 130 (80% power), 174 (90% power)
 75% of observed effect: n per arm = 257 (80% power), 343 (90% power)
 50% of observed effect: n per arm = 631 (80% power), 844 (90% power)
power.prop.test: 129.8 
Simulated power at n = 130 per arm: 0.815 (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. Analyses Reported by the Sponsor

The registry’s reported analysis entries list a binomial test for each of the three groups and p < 0.001 for each entry. Those entries do not show an estimated parameter or confidence interval, and the registry record does not explain the null hypothesis or other details of the tests. They therefore cannot be read as direct reported tests of the pairwise contrasts described by the recalculated risk differences.

The pairwise estimates in the posted comparisons are simple unadjusted recalculations from group-level summaries. The registry flags a discrepancy between these recalculations and the sponsor’s own analysis. Where that discrepancy applies, the sponsor’s own analysis takes precedence. The recalculated estimates remain useful for understanding the direction and uncertainty of contrasts derived from the posted counts, but they should not be presented as the sponsor’s prespecified analysis or as a correction to it.

The registry record does not include enough information to reconcile the analyses. In particular, it does not report the full statistical methods, tested hypotheses, handling of missing primary outcomes, or any adjustment used by the sponsor. Without those details, there is no sound basis for attributing the discrepancy to a particular method or assumption. Readers should distinguish the sponsor’s reported testing from the independent, unadjusted recalculation and avoid treating the latter as definitive when they do not agree.

15. Multiplicity, Missing Data and Analysis Populations

The study record lists one primary endpoint and several secondary outcome domains, and the posted results include comparisons across treatment groups. Repeated testing across multiple endpoints and contrasts raises a multiplicity question: the more hypotheses examined, the greater the opportunity for chance findings to appear statistically notable. A prespecified strategy can define which tests are confirmatory, how error rates are controlled, and how results should be interpreted in sequence.

Such a strategy is not reported in the registry record. The recalculated comparisons are unadjusted, and the reported binomial-test entries do not explain how they relate to the pairwise comparisons or to the study’s full set of outcomes. Thus, the p-values should not be interpreted as if family-wise error or another multiplicity concern had been addressed. The registry record also does not report whether secondary endpoints were formally confirmatory or exploratory.

The primary population is described as the Full Analysis Set: participants randomized into the study who received at least 1 dose of study drug. The registry record does not give a fuller account of how participants with missing SVR12 measurements, treatment discontinuation, or other deviations were handled. It also does not report whether an imputation method, missing-as-failure rule, sensitivity analysis, or alternative analysis population was used. Those choices can affect binary outcome estimates and their interpretation.

Randomization and the stated analysis population provide important context, but do not answer questions about missing observations or deviations from assigned treatment. The record does not report detailed eligibility exclusions after randomization, protocol deviations, or the population used for every secondary and safety result. Those omissions limit the ability to assess the robustness of all posted estimates and to compare analysis populations across outcomes.

The registry record does not report interim analyses, stopping rules, a detailed prespecified statistical analysis plan, or the original sample-size justification. These items should not be inferred from the completed status or from the posted p-values. Their absence from the record limits assessment of how the analysis strategy was specified before outcomes were observed.

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: sepsis (3.4%), gastrointestinal haemorrhage (3.3%), hepatocellular carcinoma (3.3%), urinary tract infection (2.3%), hyponatraemia (2.3%).

The registry reports serious adverse events for each treatment group as counts among the listed groups: 17 of 90 in the 12-week sofosbuvir/velpatasvir group, 14 of 87 in the 12-week sofosbuvir/velpatasvir plus ribavirin group, and 16 of 90 in the 24-week sofosbuvir/velpatasvir group. Other adverse events are also counted, with 65 of 90, 74 of 87, and 61 of 90 reported for the respective groups. These figures describe events recorded in the groups; they do not establish that study treatment caused an event.

The serious-event terms listed most often include sepsis, gastrointestinal haemorrhage, hepatocellular carcinoma, urinary tract infection, hyponatraemia, and hepatic encephalopathy, with the percentages stated in the registry. A term’s appearance among the listed serious events does not show whether it was related to study treatment. The registry record does not report death counts in the posted safety data, so they cannot be characterized from this information.

Safety interpretation depends on definitions, observation time, event ascertainment, and clinical context. The registry record does not give detailed comparative safety analyses or a complete account of exposure-adjusted event rates. Counts across groups should therefore be read descriptively, not as proof of a safety difference or equivalence.

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

The posted primary results describe SVR12 in adults with chronic HCV infection and Child-Pugh class B cirrhosis who received one of the three study regimens. They show the observed group percentages and the uncertainty around those estimates. The recalculated comparison with ribavirin has a positive risk-difference estimate with an interval above zero, while the recalculated comparison with the 24-week regimen has an interval that includes zero. These are unadjusted calculations and must be considered alongside the registry’s reported analysis and the stated discrepancy.

The results do not establish that one regimen is universally preferable, that two regimens are equivalent, or that the observed estimates will apply to populations not represented in this study. The record concerns a specific disease and cirrhosis class, specific regimens, and a defined post-treatment virologic endpoint. The study was open-label, and complete details about missing data, multiplicity, and the sponsor’s analysis are not reported in the registry record.

SVR12 is a laboratory-defined response measure at a specific follow-up time. It does not alone describe longer-term liver function, symptoms, quality of life, all safety outcomes, or later clinical events. The listed secondary outcomes address some additional questions, but the registry record does not provide complete numeric results for all of them in the registry record for this analysis. Safety event counts also require caution because event occurrence does not by itself establish treatment causation.

Statistical significance and clinical importance are different questions. A p-value summarizes compatibility with a null hypothesis under a test; it does not state whether a difference matters to patients. The registry record does not report a minimum clinically important difference or enough clinical context to decide that question. The most defensible reading is therefore limited: the posted data estimate response and safety outcomes for the study groups, with uncertainty and analysis limitations that should remain visible.

18. Why This Trial Matters Statistically

This trial raises several useful statistical issues. Its randomized, parallel-group design supports comparisons among three assigned regimens, but the interpretation still depends on the exact endpoint, analysis population, and analysis method. The primary outcome is a binary virologic response at a fixed post-treatment time, so both group percentages and between-group differences matter. Looking only at the group percentages would not fully describe uncertainty in the contrasts.

The registry also illustrates why sponsor-reported analyses and recalculations from summary data should be kept distinct. The recalculated pairwise comparisons are transparent but unadjusted, and a discrepancy is flagged. The sponsor’s own analysis takes precedence where the results differ. Without the analysis details, an independent recalculation cannot settle why the findings differ or replace the planned analysis.

Multiplicity and incomplete reporting are important to interpretation. Several outcomes and comparisons are listed, but a multiplicity strategy, missing-data approach, interim analyses, and original sample-size justification are not reported in the registry record. Those details affect how strongly individual p-values can support confirmatory claims and how robust the reported estimates are.

Finally, planning illustrations based on observed effects are not evidence of observed power and do not recover the original study design rationale. They show how hypothetical sample-size needs change when the target effect changes under stated assumptions. Keeping that planning exercise separate from interpretation of the completed trial helps prevent post hoc power calculations from being mistaken for evidence about the certainty of its findings.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The record leaves important details about the statistical analysis unavailable. It does not report the sponsor’s full model or testing procedure, the reason for the discrepancy with recalculated comparisons, or the missing-data method for SVR12. It also does not report a multiplicity strategy, a detailed prespecified analysis plan, interim analyses, or the original sample-size justification. These omissions limit assessment of whether the posted tests match the intended confirmatory questions and how sensitive the estimates are to analytic choices.

The study was open-label, and the registry record does not describe whether endpoint assessment was masked or what safeguards were used to limit potential assessment bias. The posted primary endpoint is a laboratory-defined outcome, but that does not answer questions about all other clinical outcomes. Complete numeric results for all listed secondary domains are not reported in the registry record.

The safety information is descriptive. Detailed exposure-adjusted analyses, treatment attribution, and death counts are not reported in the posted safety data. Event counts alone cannot establish a causal relationship or demonstrate comparable safety. The record also does not provide enough detail to determine how observation time or incomplete safety follow-up may have affected group comparisons.

Finally, the findings apply directly to the study’s specified population and regimens. The registry record does not establish generalizability to populations with different disease characteristics or to treatment approaches not studied. The primary outcome’s timing and definition also constrain what can be concluded: SVR12 is not a comprehensive measure of long-term liver outcomes, all aspects of patient experience, or later events.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Sofosbuvir/Velpatasvir Fixed-Dose Combination in Adults With Chronic HCV Infection and Child-Pugh Class B Cirrhosis — NCT02201901.
• Registry record last updated 2018-11-15; status last verified 2016-10.
• Results first posted 2016-12-14.
• 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

NCT02201901 is a completed phase 3, randomized, open-label, parallel-group study in adults with chronic HCV infection and Child-Pugh class B cirrhosis. The registry lists enrollment of 268 and three regimens: sofosbuvir/velpatasvir for 12 weeks, sofosbuvir/velpatasvir plus ribavirin for 12 weeks, and sofosbuvir/velpatasvir for 24 weeks.

The primary endpoint is SVR12, defined as HCV RNA below the lower limit of quantitation 12 weeks after the last dose. The posted group percentages are 83.3%, 94.3%, and 87.8%, respectively, with 95% confidence intervals reported for each. Recalculated unadjusted comparisons are distinct from the sponsor’s analyses; the registry flags a discrepancy, and the sponsor’s own analysis takes precedence where results differ.

The record lists additional virologic and liver-related outcomes and descriptive safety counts. Important analysis details, including missing-data handling, multiplicity, and the original sample-size justification, are not reported in the registry record.