A Study of Safety and Efficacy of Vaniprevir Administered With Pegylated-Interferon and Ribavirin in Japanese Participants With Chronic Hepatitis C Infection (7009-016): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Safety and Efficacy of Vaniprevir Administered With Pegylated-Interferon and Ribavirin in Japanese Participants With Chronic Hepatitis C Infection (7009-016) (NCT00880763), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving Rapid Viral Response.

2. Clinical Question

3. Trial Design

This was a Phase II, randomized, double-masked, parallel-group, placebo-controlled study. It enrolled 90 participants and is recorded as completed. The registry dates the study start to 2009-04-20 and primary completion to 2010-06-03. It identifies the participants as Japanese patients with chronic hepatitis C who had prior treatment experience.

Participants were assigned to one of four treatment groups: vaniprevir 200 mg, 600 mg, or 1200 mg, or placebo. All groups also received pegylated interferon and ribavirin. The three vaniprevir regimens corresponded to 100 mg, 300 mg, or 600 mg twice daily, respectively, for 28 days; placebo was also given twice daily for 28 days. The registry says the background pegylated interferon and ribavirin could continue through Week 6 or, at investigators’ discretion, up to Week 72. Details of how randomization was generated, how allocation was concealed, and who remained masked are not reported in the registry record.

The primary efficacy result was assessed at Week 4 in a per-protocol population. The registry defines that population by excluding participants with important protocol deviations that could substantially affect the primary efficacy analysis. The primary outcome was the percentage achieving rapid viral response, defined as undetectable HCV RNA at Week 4. The registry also lists secondary measures of early HCV RNA reduction and adverse events.

The original design’s planned allocation by arm, target effect, sample-size justification, and statistical analysis plan are not reported in the registry record. The listed enrollment of 90 is the study-wide enrollment, while the primary outcome groups have the denominators reported for their per-protocol analyses.

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: Initial treatment period (Part 1) includes up through Week 6; Extension period (Part 2) includes from Week 6 through Week 96.

Initial Treatment Period (Part 1)

Extension Period (Part 2)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per protocol population excludes participants for important deviations from the protocol that may substantially affect the results of the primary efficacy 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: All randomized participants

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Rapid Viral Response, measured over Week 4.

The primary endpoint was the percentage of participants achieving rapid viral response at Week 4. A response meant that HCV RNA was undetectable at that visit. This binary outcome records whether each participant met the response definition, rather than the size of a continuous change in viral load. It therefore provides a direct count-based comparison of response proportions between each vaniprevir group and placebo.

HCV RNA was measured with the Roche COBAS TaqMan HCV Auto assay. The registry reports a limit of quantification of 1.2 log IU/mL (15 IU/mL) and a limit of detection of <1.2 log IU/mL, with no specific value. “Undetectable” is consequently an assay-based classification; it does not mean that the virus was established to be absent from the body. The reported response is tied to the Week 4 measurement and assay definition, not to a later sustained response.

General: binary outcomes are often useful when a trial asks how many participants cross a clinically defined response threshold. Their interpretation depends on the threshold, timing, assay, and analysis population. In this study, the endpoint answers whether the Week 4 viral measurement met the stated undetectable criterion. It does not by itself describe longer-term viral status, symptoms, complications, or comparative safety.

7. Results Posted in the Registry

• Vaniprevir 200 mg + Peg-IFN + Ribavirin: 86.4% (19/22) versus 20.0% (4/20) on control; risk difference 66.4 percentage points (95% CI 43.7 to 89.0), risk ratio 4.32 (1.77–10.54); unadjusted two-proportion z-test p = <0.001.
• Vaniprevir 600 mg + Peg-IFN + Ribavirin: 95.0% (19/20) versus 20.0% (4/20) on control; risk difference 75.0 percentage points (95% CI 55.0 to 95.0), risk ratio 4.75 (1.97–11.48); unadjusted two-proportion z-test p = <0.001.
• Vaniprevir 1200 mg + Peg-IFN + Ribavirin: 76.2% (16/21) versus 20.0% (4/20) on control; risk difference 56.2 percentage points (95% CI 30.9 to 81.5), risk ratio 3.81 (1.54–9.45); unadjusted two-proportion 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.

Percentage of Participants Achieving a > or = 2-log10 Decrease in HCV RNA From Baseline to Week 4

• 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:
  • Vaniprevir 200 mg + Peg-IFN + Ribavirin: 100.0% (22/22) versus 95.0% (19/20) on control; risk difference 5.0 percentage points (95% CI -4.6 to 14.6), risk ratio 1.05 (0.95–1.16); unadjusted two-proportion z-test p = 0.288.
  • Vaniprevir 600 mg + Peg-IFN + Ribavirin: 100.0% (20/20) versus 95.0% (19/20) on control; risk difference 5.0 percentage points (95% CI -4.6 to 14.6), risk ratio 1.05 (0.95–1.16); unadjusted two-proportion z-test p = 0.311.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vaniprevir 200 mg + Peg-IFN + Ribavirin 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 Vaniprevir 600 mg + Peg-IFN + Ribavirin and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving a > or = 3-log10 Decrease in HCV RNA From Baseline to Week 4

• 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:
  • Vaniprevir 200 mg + Peg-IFN + Ribavirin: 100.0% (22/22) versus 85.0% (17/20) on control; risk difference 15.0 percentage points (95% CI -0.6 to 30.6), risk ratio 1.18 (0.98–1.41); unadjusted two-proportion z-test p = 0.059.
  • Vaniprevir 600 mg + Peg-IFN + Ribavirin: 100.0% (20/20) versus 85.0% (17/20) on control; risk difference 15.0 percentage points (95% CI -0.6 to 30.6), risk ratio 1.18 (0.98–1.41); unadjusted two-proportion z-test p = 0.072.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vaniprevir 200 mg + Peg-IFN + Ribavirin 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 Vaniprevir 600 mg + Peg-IFN + Ribavirin and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the Week 4 efficacy picture beyond the primary undetectable-RNA threshold. They include participants reaching specified log10 decreases in HCV RNA, the change in HCV RNA from baseline, and adverse-event measures. The posted results for the two threshold outcomes show a broad pattern of frequent early viral-load reductions in all groups, including placebo plus pegylated interferon and ribavirin. This is consistent with the primary finding being a stricter, assay-based response threshold rather than the only measure of viral change.

The secondary threshold comparisons do not establish that all vaniprevir groups differed from placebo. Their reported adjusted intervals include values on either side of zero for the comparisons with available estimates, and the registry does not post every possible group comparison. The endpoint-specific values and estimates are reported with the secondary results; the overall pattern should not be collapsed into a single claim about all secondary outcomes.

These secondary measures complement, but do not replace, the primary Week 4 rapid viral response analysis. The measures use different thresholds or a different expression of viral change, and adverse-event outcomes address safety rather than efficacy. A finding on one measure does not automatically imply the same finding on another.

Unadjusted secondary results carry less weight for confirmatory claims because multiple outcomes and comparisons create more opportunities for chance findings. General: when many hypotheses are tested, the chance of at least one apparently notable result can increase unless the analysis accounts for multiplicity. The registry record does not report a multiplicity adjustment for the secondary outcomes, so their role is best understood as supportive or exploratory rather than as independent confirmation of the primary result. The record also does not provide results for all five listed secondary outcomes in the posted result data.

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

• Percentage of Participants Achieving a > or = 2-log10 Decrease in HCV RNA From Baseline to Week 4
• Percentage of Participants Achieving a > or = 3-log10 Decrease in HCV RNA From Baseline to Week 4
• Change From Baseline in HCV RNA in log10 at Week 4
• Number of Participants Who Experienced at Least One Adverse Event
• Number of Participants Who Discontinued Study Drug Due to an Adverse Event

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the Week 4 rapid viral response definition or did not. The registry reports the percentage meeting that definition within each group. A percentage makes the event frequency easy to compare across groups, while the number of analyzed participants gives context for how much information supports each percentage. The primary outcome analysis used a per-protocol population, which excluded participants with important deviations that could substantially affect the efficacy analysis.

What does a risk difference describe?

General: a risk difference subtracts one group’s event proportion from another group’s event proportion. It expresses the absolute separation between response probabilities, rather than a relative comparison. A positive difference for this endpoint means a larger observed response proportion in the vaniprevir group than in the placebo group. The registry’s reported analysis expresses these differences in percentage points and labels them adjusted differences in percent.

The sponsor’s reported method was Miettinen and Nurminen. This is a method for estimating and testing differences between binomial proportions. The registry lists a 95% confidence interval and a p-value for each vaniprevir-versus-placebo comparison. The reported intervals and tests are the sponsor’s results and should be distinguished from recalculated, unadjusted comparisons based on the posted counts.

What does the p-value contribute?

General: a p-value measures how incompatible the observed data are 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 a difference. The primary comparisons have reported p-values of <0.001. Interpretation should consider these alongside the effect estimates, confidence intervals, endpoint definition, analysis population, and number of comparisons. Whether the reported primary p-values were adjusted for multiple testing is not reported in the registry record.

Why are recalculations distinct?

The recalculated risk differences use the response counts and denominators posted for the groups and are unadjusted. They are a transparent arithmetic check based on those summary data, but they do not reproduce every feature of an analysis method or any adjustments that may have been used by the sponsor. The sponsor’s own reported estimates and tests take precedence. The registry record does not flag a discrepancy between the posted results and the recalculations.

How should missing outcomes be considered?

The primary outcome description says the Data-As-Observed approach was used to handle missing data. This identifies the approach named in the registry, but the record does not give a detailed account of missing observations by group, assumptions about missingness, or sensitivity analyses. General: an observed-data approach uses the measurements available for analysis; if missingness is related to response or treatment, the analyzed participants may not represent all randomized participants. That possibility cannot be quantified from the registry record.

What does the endpoint’s timing imply?

The primary assessment was at Week 4, with undetectable HCV RNA as the threshold. The method therefore addresses a short-term, assay-defined response. The secondary measures also include changes in HCV RNA at Week 4 and adverse-event counts. The registry does not establish that the Week 4 endpoint predicts sustained response or later clinical outcomes in this trial. General: an endpoint can be suitable for answering a focused trial question while not covering every outcome important to patients or clinicians.

The record identifies the trial as randomized, double-masked, and parallel-group, but does not report the random sequence method, concealment procedure, masking details, or protocol deviations by group. It also does not report an interim analysis plan or the original statistical analysis plan. These omissions limit how fully a reader can audit design implementation and analysis choices from the registry record alone.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence intervals for the primary adjusted differences are 37.0 to 82.8 percentage points for 200 mg versus placebo, 47.6 to 89.0 for 600 mg versus placebo, and 24.9 to 76.0 for 1200 mg versus placebo. Each interval lies above zero, indicating that the reported estimates are compatible with a positive difference under the stated method and interval construction. The intervals also span a range of plausible effect sizes, so the point estimates should not be treated as exact values.

The 1200 mg comparison has the widest reported interval, from 24.9 to 76.0, while the other intervals also cover broad ranges. The primary analyzed group sizes were 22, 20, 21, and 20. General: confidence intervals convey both the estimated direction and the uncertainty around an estimate. Their width depends on the data and the method; broader intervals indicate less precision than narrower intervals, all else equal. An interval is not a guarantee that the true effect lies inside it, nor does it account for unreported sources of uncertainty such as analysis choices or missing-data assumptions.

Because the outcome is a proportion, the same observed percentage can have different precision depending on the number of participants and response counts. The small analyzed groups make it important to consider the interval bounds rather than focusing only on the percentages or p-values. The confidence intervals apply to the sponsor’s adjusted differences as reported; they should not be confused with intervals from the separate unadjusted recalculations.

The registry reports no confidence interval for the individual group response percentages in the primary results. The uncertainty pertains to the between-group comparisons. Long-term response, outcomes outside the Week 4 assessment, and safety differences are not resolved by these efficacy intervals.

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 original design justification for this trial. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For these binary outcome comparisons, the figures mean participants per arm. The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are design calculations, not guarantees of a result and not descriptions of the actual enrollment in this study.

The planning rows consider 100%, 75%, and 50% of the observed effect. A smaller target effect requires more participants to distinguish it from chance variation at the same stated power and significance level. Consequently, planning around a fraction of the observed effect produces larger per-arm estimates than planning around the full observed effect. That is useful because effects observed in a particular study may be larger or smaller than effects seen in a future study.

These calculations are not observed power. They do not tell whether the completed trial was adequately powered based on its actual design, nor do they replace the confidence intervals around the posted estimates. The registry’s original planning assumptions, including the effect the investigators intended to detect, are not reported in the registry record.

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 = 0.200; treatment proportion p₁ = 0.864; average p̄ = 0.532.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7057 = 1.3831.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5270 = 0.4436.
4. n = (1.3831 + 0.4436)² / (0.6636)² = 7.6, rounded up to 8 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 <- 0.2                          # control proportion
p1 <- 0.863636363636364                          # 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(880763)
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 = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 15 (80% power), 19 (90% power)
 50% of observed effect: n per arm = 32 (80% power), 43 (90% power)
power.prop.test: 7.6 
Simulated power at n = 8 per arm: 0.883 (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 sponsor-reported primary analysis used the Miettinen and Nurminen method. It reports adjusted differences in percent with 95% confidence intervals and p-values for each vaniprevir dose compared with placebo. Those reported estimates and tests are the primary inferential results to use when describing the sponsor’s analysis.

The separate recalculated comparisons are unadjusted calculations from the posted response counts and denominators. They provide a simple check of the direction and approximate size of the group separation, but they are not the same analysis as the sponsor’s method. They should not be substituted for the sponsor’s adjusted estimates or treated as a correction to them. The registry record does not flag a discrepancy, so there is no reported conflict requiring a recalculation to take precedence.

For each dose, both approaches indicate a higher observed Week 4 response proportion than placebo. The sponsor’s reported adjusted differences are 65.1, 74.5, and 55.4 percentage points for 200 mg, 600 mg, and 1200 mg, respectively; each is reported with p < 0.001. The recalculations use different estimation procedures, so numerical differences between their estimates and the sponsor’s values do not on their own imply an error.

The registry does not describe all details of the sponsor’s analysis plan, including any multiplicity procedure. The result should therefore be attributed to the analysis reported in the registry, with its stated method and population, rather than interpreted as a full reconstruction of the original statistical plan.

15. Multiplicity, Missing Data and Analysis Populations

The primary question involved three vaniprevir dose groups, each compared with the same placebo group. The registry reports a p-value and confidence interval for each of these comparisons. It does not report whether the primary comparisons were adjusted for multiplicity, whether one dose was designated as the principal comparison, or how the family of tests was defined. The original statistical analysis plan is not reported in the registry record.

General: testing several doses against one control creates multiple opportunities for a nominally small p-value. Multiplicity procedures can control the overall false-positive risk across a family of comparisons, but the registry’s posted results do not identify such a procedure. This does not erase the reported estimates; it means the reported p-values should be interpreted with awareness that the handling of multiple primary comparisons is not documented.

The registry lists several secondary outcomes and reports only some of the analyses in the posted results. Whether secondary outcomes were prespecified in a hierarchy, whether testing was adjusted, and how missing secondary measurements were handled are not reported in the registry record. General: secondary analyses are often useful for describing a broader outcome pattern, but unadjusted testing across many outcomes is less persuasive as confirmatory evidence.

For the primary outcome, the record states that the Data-As-Observed approach was used for missing data. It does not give group-specific missing outcome counts, the reasons for missingness, or sensitivity analyses under alternative assumptions. A per-protocol population was used, excluding important protocol deviations that could substantially affect the primary efficacy analysis. The record does not give enough detail to assess how many participants were excluded or how exclusion affected comparability after randomization.

Randomization and double masking are stated design features, but implementation details and the extent of masking are not reported in the registry record. Interim analyses, stopping boundaries, and other monitoring procedures are also not reported in the registry record. These omissions leave uncertainty about analysis decisions and implementation, rather than changing the values explicitly posted for the endpoint.

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: disseminated intravascular coagulation (4.5%), cataract (4.5%), inguinal hernia (4.5%), bacterial infection (4.5%), infective spondylitis (4.5%).

The serious adverse-event results report 2 affected participants among 23 at risk in the 200 mg group, 2 among 22 in the 600 mg group, 0 among 23 in the 1200 mg group, and 2 among 22 in the placebo group. These are participant counts with at least one serious adverse event, not counts of all individual events. The registry also lists serious-event terms, each at 4.5%: disseminated intravascular coagulation, cataract, inguinal hernia, bacterial infection, infective spondylitis, and acute renal failure.

For the separate any-adverse-event measure, the registry reports 23 affected participants among 23 at risk in each of the three vaniprevir groups and 22 among 22 in the placebo group. These counts should not be confused with serious adverse events; the categories address different levels of event severity. The registry does not report death counts in the posted safety data.

General: small group sizes make safety comparisons imprecise, particularly for uncommon serious events. A count of zero in one group does not establish that an event cannot occur, and these counts alone do not establish whether an event was caused by treatment. The registry record does not report event attribution or provide detailed event narratives, duration, or outcome for the listed serious events.

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

The results show that, in the analyzed participants, the Week 4 rapid viral response percentage was higher in each vaniprevir group than in the placebo group receiving the same background medicines. The sponsor-reported adjusted comparisons were positive, their 95% confidence intervals were above zero, and the registry reports p < 0.001 for each. These findings describe the short-term endpoint and the analysis reported for this Phase II study.

They do not demonstrate that every participant receiving vaniprevir would respond, or that the observed percentages would be reproduced in another population. They do not establish a sustained response after Week 4, because the primary endpoint is an assessment at that time point. The registry record does not provide a long-term virologic outcome in the primary results, nor does the Week 4 result establish changes in symptoms, complications, or other patient outcomes.

The results also do not establish that one vaniprevir dose is superior to another. Each sponsor-reported comparison is against placebo; the registry does not report a direct randomized comparison among the vaniprevir dose groups. The observed percentages vary across the three dose groups, but comparing those percentages informally is not equivalent to a prespecified dose-comparison test.

Safety should be considered separately from the efficacy endpoint. Serious adverse events were reported in the treatment groups and placebo group, and any adverse event was reported for all participants at risk in the posted safety groups. The small groups and limited safety detail do not support a precise comparative assessment of uncommon harms. General: a trial’s efficacy result and its safety result answer different questions, and neither should be used alone to characterize the overall balance of effects.

The registry identifies the study as randomized and double-masked, but the record does not report the detailed methods for those procedures, the original sample-size justification, or a full analysis plan. The strongest interpretation is therefore bounded: the posted primary analysis indicates a clear Week 4 response separation in this trial, while its longer-term meaning, generalizability, and comparative safety remain uncertain from the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition matters. “Rapid viral response” was defined by an assay-based threshold at Week 4, while the secondary outcomes used specified magnitudes of HCV RNA reduction. Those measures describe related but distinct aspects of early viral change. A large difference on the primary threshold does not mean that every measure of viral response, or every later outcome, has the same pattern.

It also shows the importance of distinguishing a group percentage from a comparative estimate. The response proportions describe each analyzed group; the sponsor’s adjusted difference and confidence interval describe the comparison with placebo and its uncertainty. Reading the estimate together with the interval gives more information than a p-value alone. The unadjusted recalculation is another useful statistical lens, but it should not replace the sponsor’s reported analysis.

The study’s four-group design makes multiplicity relevant: three vaniprevir doses were each compared with placebo. The record reports the separate comparisons but does not state whether or how multiple testing was addressed. This is a practical reminder that interpretation depends not only on numerical results but also on the analysis plan and testing framework.

Finally, the record distinguishes efficacy analysis from safety reporting. The primary outcome used a per-protocol population and an observed-data approach, while safety counts use their own at-risk denominators. A reader should attend to the population and denominator for each result rather than assuming that the same participants contribute to every analysis. These statistical distinctions help keep a short-term efficacy signal, uncertainty, and safety evidence in their proper scope.

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 primary endpoint is limited to an assay-defined measurement at Week 4. It does not establish sustained virologic response or long-term clinical outcomes. The registry record reports the assay limits and outcome definition but does not provide later primary efficacy results in the posted data described for this analysis.

The efficacy analysis used a per-protocol population rather than a stated all-randomized population. Although the record defines the per-protocol exclusions in general terms, the number and distribution of excluded participants and the reasons for deviations are not reported in the registry record. The primary endpoint also used a Data-As-Observed approach; the group-specific missing outcome counts and sensitivity analyses are not reported in the registry record.

The primary analysis compares each dose with placebo, but the registry does not report direct comparisons among doses. No firm dose-response conclusion follows from the observed group percentages alone. The registry also does not state whether multiplicity was addressed across the primary dose comparisons or the secondary outcomes.

The study enrolled 90 participants, and the primary outcome denominators were 22, 20, 21, and 20. Such group sizes limit precision and the ability to characterize uncommon outcomes. Safety reporting includes counts of participants with serious and any adverse events, but detailed event attribution, clinical course, and death counts are not reported in the registry record.

Important design and analysis details are also absent: the original sample-size justification, allocation concealment and randomization procedures, masking implementation, interim analysis procedures, and full statistical analysis plan are not reported in the registry record. These limits do not invalidate the posted results, but they constrain independent assessment of analysis choices, generalizability, and the robustness of conclusions beyond the recorded Week 4 comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Safety and Efficacy of Vaniprevir Administered With Pegylated-Interferon and Ribavirin in Japanese Participants With Chronic Hepatitis C Infection (7009-016) — NCT00880763.
• Registry record last updated 2018-10-09; status last verified 2018-09.
• Results first posted 2014-09-29.
• 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

NCT00880763 is a completed Phase II, randomized, double-masked, parallel-group, placebo-controlled study sponsored by Merck Sharp & Dohme LLC. It enrolled 90 Japanese treatment-experienced participants with chronic hepatitis C. The study compared vaniprevir at 200 mg, 600 mg, or 1200 mg with placebo, with all groups receiving pegylated interferon and ribavirin.

The primary outcome was rapid viral response at Week 4, defined as undetectable HCV RNA, and the primary efficacy analysis used a per-protocol population with a Data-As-Observed approach to missing data. The sponsor-reported adjusted comparisons favored each vaniprevir group over placebo for this endpoint. The registry also posts early viral-load reduction outcomes and adverse-event counts. The results are specific to the stated analysis, endpoint, and follow-up time; longer-term outcomes and several design and analysis details are not reported in the registry record.