Grazoprevir (MK-5172) and Elbasvir (MK-8742) Combination for Chronic Hepatitis C Virus (HCV) Genotypes 1, 4, and 6 (MK-5172-065): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Grazoprevir (MK-5172) and Elbasvir (MK-8742) Combination for Chronic Hepatitis C Virus (HCV) Genotypes 1, 4, and 6 (MK-5172-065) (NCT02252016), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Sustained Virologic Response 12 Weeks After Completing Study Therapy (SVR12).

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, parallel-group phase III trial described as multi-site and placebo-controlled. The registry record lists 159 participants enrolled and a completed study status. The recorded start date is 2014-10-22, and the primary completion date is 2015-12-07. Merck Sharp & Dohme LLC is listed as the sponsor.

The immediate-treatment arm received grazoprevir 100 mg plus elbasvir 50 mg once daily for 12 weeks, followed by a 24-week safety follow-up period. The deferred-treatment arm received placebo during a 12-week period and then began open-label treatment with the combination for 12 weeks. This sequencing matters when interpreting arm-level response estimates: the deferred group was not a permanently untreated control group, and the primary endpoint was measured after completion of study therapy.

Although allocation was randomized and masking was double, the registry record does not report details such as the randomization procedure, allocation concealment, stratification factors, or the exact maintenance of masking through the deferred-treatment transition. These aspects should not be inferred from the design labels alone. The reported primary response population included treated participants after excluding discontinuations for reasons unrelated to treatment or HCV response; it was therefore not simply every person enrolled.

The study addressed participants with chronic HCV genotypes 1, 4, or 6 and inherited blood disorders, with and without HIV co-infection. The enrollment total and the numbers contributing to the posted primary outcome differ, and the record does not give a complete accounting of every reason for that difference. The original design assumptions, including any planned power calculation or target effect, are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consists of all treated participants in both arms other than those who discontinued with reasons unrelated to the treatment regimen or HCV response.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Sustained Virologic Response 12 Weeks After Completing Study Therapy (SVR12), measured over 12 weeks after completing study therapy (Week 24).

The primary endpoint was the percentage of participants achieving sustained virologic response 12 weeks after completing study therapy, or SVR12. A participant counted as achieving this endpoint if HCV RNA was below the lower limit of quantification 12 weeks after therapy ended. The registry specifies that HCV RNA was measured using the Roche COBAS Taqman HCV Test v2.0 (High Pure System), with a lower limit of quantification of <15 IU/mL.

SVR12 is a binary outcome at the participant level: each person either met the stated RNA criterion at the specified follow-up or did not. Reporting the percentage therefore describes how common the endpoint was in the analysis population. The accompanying confidence interval conveys uncertainty around that percentage; it does not show the range of individual participants’ RNA values.

The endpoint is used to assess whether the specified virologic response was present at a defined time after treatment completion. Its timing is important: the registry defines the endpoint relative to the end of each participant’s study therapy, not simply by a common calendar date. The primary hypothesis in the brief summary concerned whether the treated proportion was greater than the reference rate of 40%. The posted arm comparison instead addresses the estimated contrast between the immediate- and deferred-treatment groups. These are not interchangeable statistical questions.

The registry also lists SVR24, assessed 24 weeks after completing study therapy, as a secondary outcome. That later measurement offers information about response at a subsequent follow-up point, but it does not change the definition of the primary endpoint.

7. Results Posted in the Registry

• Deferred Treatment: 91.8% (45/49) versus 93.5% (100/107) on control; risk difference -1.6 percentage points (95% CI -10.6 to 7.4), risk ratio 0.98 (0.89–1.08); unadjusted two-proportion z-test p = 0.714.

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 Sustained Virologic Response 24 Weeks After Completing Study Therapy (SVR24)

• 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:
  • Deferred Treatment: 91.8% (45/49) versus 90.7% (97/107) on control; risk difference 1.2 percentage points (95% CI -8.3 to 10.6), risk ratio 1.01 (0.91–1.12); unadjusted two-proportion z-test p = 0.810.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Deferred Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists SVR24 as a secondary outcome, measured 24 weeks after completing study therapy. Its arm-level response estimates remain close, and the posted risk-difference interval includes zero. At a broad level, that pattern is consistent with the primary endpoint’s lack of a clearly resolved between-arm contrast. It does not independently establish that the two arm results are equivalent, and it does not replace the primary SVR12 analysis.

Secondary endpoints can help describe whether the general pattern persists at a different follow-up time, but they usually carry less inferential weight than a prespecified primary endpoint. This is partly because multiple outcomes or comparisons create more opportunities for apparently notable results to arise by chance. A multiplicity strategy can address that concern by specifying how error rates are controlled across tests. The registry record does not report such a strategy or a multiplicity-adjusted analysis.

The registry identifies one posted secondary outcome and does not list reported analyses for it. The absence of a listed analysis should not be interpreted as evidence that no analyses were conducted; it means the registry record does not report them. Likewise, the presence of a secondary endpoint does not show whether it was prespecified in the original statistical plan, how missing values were handled, or what inferential role was intended.

Accordingly, the secondary result is best treated as supporting descriptive context around the primary response findings. It is not a separate confirmatory conclusion. The clinical meaning of a difference at the later follow-up would also depend on the treatment sequence and endpoint timing, not only on whether a statistical test crosses a conventional threshold.

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

• Percentage of Participants Achieving Sustained Virologic Response 24 Weeks After Completing Study Therapy (SVR24)

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary, because each participant is classified according to whether SVR12 was achieved. For this kind of endpoint, an arm-level percentage is the proportion meeting the endpoint among the participants included in that arm’s analysis. The registry reports these percentages together with 95% confidence intervals. A confidence interval is an interval estimate of the uncertainty around an estimated quantity under the statistical procedure used; it is not a statement that a particular percentage of individual observations fall inside the interval.

What does the between-arm estimate represent?

The posted comparison is a risk difference: the response proportion in the deferred-treatment arm minus the response proportion in the immediate-treatment arm. A risk difference of zero corresponds to equal estimated proportions. Negative values indicate a lower estimated proportion in the deferred-treatment arm, and positive values indicate a higher estimated proportion in that arm. The reported interval runs from -0.106 to 0.074 and includes zero, so the comparison is compatible with no difference as well as with differences in either direction. The unadjusted p-value is 0.714. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the analysis assumptions; it is not the probability that the null hypothesis is true.

The posted comparison also includes relative measures, the risk ratio and odds ratio, with their intervals. These are alternative ways to express an arm contrast, rather than separate outcomes. Risk differences are expressed on an absolute scale, while risk ratios and odds ratios express relative contrasts. The registry record does not report an adjusted analysis for these comparisons, so they should be understood as unadjusted comparisons rather than estimates controlling for participant characteristics.

Why distinguish the trial hypothesis from the arm comparison?

The brief summary describes a primary hypothesis that the proportion achieving SVR12 would be greater than a reference rate of 40%. That is a one-sample question about a response proportion relative to a fixed benchmark. The posted risk difference is instead a two-arm comparison. A result from one analysis does not automatically answer the other question. The registry record does not report the formal test, confidence interval, or decision rule used for the reference-rate hypothesis.

What does the analysis population mean?

The Full Analysis Set is described as all treated participants in both arms except people who discontinued for reasons unrelated to the treatment regimen or HCV response. Thus, the arm denominators for the primary outcome are 107 and 49, while the total enrollment was 159. Those numbers describe distinct stages of trial participation and analysis; they should not be treated as interchangeable. The registry record does not provide a complete participant flow or all reasons for exclusion and missing endpoint data. It also does not report the handling of missing SVR12 measurements, the imputation approach, or sensitivity analyses addressing missing outcomes.

What can be inferred from a non-significant comparison?

A non-significant p-value does not demonstrate equivalence, non-inferiority, or exact equality. Such conclusions generally depend on a prespecified margin and an analysis designed for that question. Neither a margin nor a non-inferiority or equivalence analysis is reported in the registry record. The confidence interval is useful because it displays the range of contrasts compatible with the data under the interval method, including both negative and positive values.

How should planning illustrations be understood?

The planning illustrations use the observed effect as a starting point and show sample sizes under stated assumptions. They are not the original trial’s design justification, which is not reported in the registry record. These illustrations concern hypothetical future planning, not the probability that the completed trial detected a true effect. Over-dispersion, in general, means that outcomes vary more than a model’s assumed variability allows; when present, it can make standard errors and confidence intervals that ignore it too small. The registry record does not report a specific over-dispersion assessment for these binary outcomes, so no conclusion about its presence or adjustment can be made.

The record also does not report whether interim analyses were planned or conducted, the exact statistical model used for the posted comparisons, or the prespecified multiplicity strategy. Those details are important for a full audit of inferential procedures and should not be inferred from the outcome estimates alone.

11. Confidence Intervals and Precision

The confidence intervals show that the arm-specific response percentages are estimated with meaningful uncertainty. For SVR12, the immediate-treatment estimate is 93.5%, with a 95% confidence interval from 87.0% to 97.3%. The deferred-treatment estimate is 91.8%, with a 95% confidence interval from 80.4% to 97.7%. The deferred-treatment interval is wider, consistent with its smaller analysis denominator of 49 compared with 107 in the immediate-treatment arm. The interval width reflects both the observed response pattern and the amount of information available.

For the arm contrast, the risk-difference estimate is -0.016, and its 95% confidence interval extends from -0.106 to 0.074. Because this interval includes zero and also spans differences in both directions, the data do not precisely establish the direction or size of a between-arm contrast. Its interpretation is more informative than treating the point estimate alone as definitive.

Confidence intervals are not guarantees that the true value lies inside a particular interval, nor do they show the distribution of individual outcomes. In repeated use of a valid interval procedure under its assumptions, intervals constructed in this way would cover the underlying quantity at the stated rate. The registry record does not identify the exact interval method, so no method-specific properties should be assumed beyond the reported 95% level.

For SVR24, the arm-specific intervals also overlap substantially, and the risk-difference interval includes zero. The later endpoint has its own uncertainty and should not be viewed as a precision upgrade to SVR12. Overall, the posted estimates support a descriptive account of high observed response percentages, while the confidence intervals caution against reading small differences between the arm estimates as firmly resolved.

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 planning figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is expressed as a stated fraction of the observed effect. These assumptions describe the planning illustration, not the original trial design; the registry record does not report the trial’s own sample-size justification or original design assumptions.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of obtaining a statistically significant result under the specified assumptions, if the effect used for planning were the true effect. The 90% power column uses the corresponding higher probability of detecting that specified effect. Power is a property of a planned design under assumed conditions, not a measure of whether the completed study succeeded. The planning figures are not observed power.

Rows planning for 100%, 75%, and 50% of the observed effect make the assumed target effect progressively smaller. Smaller effects are harder to distinguish from random variation, so the planning estimates require more participants per arm. The large values in these illustrations should not be read as estimates of the actual sample size needed under every possible design: they depend on the observed effect, the fraction selected, the statistical assumptions, and the chosen power level.

The same interpretation applies to the secondary endpoint planning figures. They are hypothetical planning estimates derived from the posted effect and stated assumptions, rather than a reconstruction of the trial’s original sample-size calculation. The record does not report whether the sponsor used these assumptions when designing the 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 = 0.935; treatment proportion p₁ = 0.918; average p̄ = 0.926.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3691 = 0.7234.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3689 = 0.3105.
4. n = (0.7234 + 0.3105)² / (-0.0162)² = 4,067.3, rounded up to 4,068 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 <- 0.934579439252336                          # control proportion
p1 <- 0.918367346938776                          # 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(2252016)
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 = 4,068 (80% power), 5,445 (90% power)
 75% of observed effect: n per arm = 7,048 (80% power), 9,435 (90% power)
 50% of observed effect: n per arm = 15,444 (80% power), 20,674 (90% power)
power.prop.test: 4067.3 
Simulated power at n = 4,068 per arm: 0.805 (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

Multiplicity arises when several hypotheses, endpoints, time points, subgroups, or treatment comparisons are assessed. Without an appropriate strategy, the chance of at least one false-positive finding can increase as the number of tests grows. Possible approaches include prespecifying a primary test, controlling a family-wise error rate, or treating additional analyses as exploratory. The registry record does not report a multiplicity adjustment or a detailed hierarchy of statistical tests. It is therefore not possible to determine from the record whether the posted p-values account for the full set of analyses conducted.

The primary endpoint is identified as SVR12, and SVR24 is listed as a secondary endpoint. That distinction supports giving the primary outcome greater interpretive weight, but it does not establish the complete prespecified analysis plan. The record does not report the full set of planned endpoints, subgroup analyses, interim analyses, or decision rules. These details should not be inferred from the results that happen to be posted.

Missing data are another important issue for a binary response endpoint. A participant without an observed RNA measurement at the specified follow-up cannot automatically be classified as either a responder or a nonresponder without a stated analysis rule. The Full Analysis Set definition excludes participants who discontinued for reasons unrelated to the treatment regimen or HCV response, but the registry record does not report how other missing endpoint values were handled. It also does not report imputation methods, sensitivity analyses, or the number of missing measurements by arm.

The posted denominators are 107 for immediate treatment and 49 for deferred treatment, compared with enrollment of 159. These figures indicate that the analysis population and total enrollment are not identical, but the record does not give enough detail to account for every difference. The primary population definition should therefore be kept in view when interpreting percentages, rather than assuming that all enrolled participants contributed to each outcome.

Finally, the registry record does not report the statistical analysis plan, the original sample-size justification, or whether any interim monitoring was undertaken. These omissions limit assessment of prespecification, missing-data robustness, and the control of false-positive conclusions across analyses.

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: sickle cell anaemia with crisis (3.8%), anaemia (1.9%), fall (1.9%), alanine aminotransferase increased (1.9%), aspartate aminotransferase increased (1.9%).

The serious adverse event figures are reported for the immediate-treatment group and for the deferred-treatment group during its placebo phase. Serious adverse events were recorded in 6 of 107 participants at risk in the immediate-treatment group and 6 of 52 at risk during the deferred group’s placebo phase. Other adverse events were recorded in 78 of 107 and 34 of 52 participants at risk, respectively. These counts describe participants with reported events, not necessarily the total number of separate event episodes.

The listed serious-event terms include sickle cell anaemia with crisis at 3.8%, and anaemia, fall, alanine aminotransferase increased, aspartate aminotransferase increased, and osteonecrosis each at 1.9%. The registry record does not provide context in this summary for attributing these events to treatment, and the deferred-treatment figures relate specifically to the placebo phase rather than the later open-label treatment period. The recorded death values are not reported in the registry record.

Safety counts should be read with their stated risk populations and treatment periods. They are descriptive summaries and, on their own, do not establish comparative risk or causation.

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

The posted results show high observed SVR12 percentages in both randomized groups under the registry’s analysis-population definition. The estimated difference between the groups is small in absolute terms, but its confidence interval includes zero and extends in both directions. The evidence therefore does not precisely determine whether the underlying response proportions differed, or by how much. A non-significant comparison is not proof that the groups are identical.

The trial’s stated primary hypothesis concerned whether the treated proportion exceeded a reference rate of 40%. The registry record reports the arm-specific estimates and a between-arm risk difference, but does not report a formal test against that benchmark. Those results cannot be treated as a reported test of the reference-rate hypothesis. The distinction is especially important because the two randomized groups followed different treatment sequences, with the deferred group receiving placebo initially and later receiving open-label combination treatment.

The findings apply most directly to the trial population described in the registry: participants with chronic HCV genotypes 1, 4, or 6 and inherited blood disorders, including participants with and without HIV co-infection. They do not, by themselves, establish the same response pattern in other populations or under other treatment conditions. The registry record’s analysis population also excludes certain treated participants who discontinued for reasons unrelated to treatment or HCV response.

The results do not establish a causal explanation for individual outcomes, prove an absence of adverse events, or resolve how missing measurements could affect the estimates. They also do not establish equivalence or non-inferiority, for which prespecified margins and corresponding analyses would be needed; such analyses are not reported in the registry record. The appropriate interpretation is descriptive and comparative, with uncertainty retained rather than collapsed into a claim of equality or certainty.

17. Why This Trial Matters Statistically

This trial illustrates why an endpoint’s wording and timing matter. SVR12 is defined relative to completion of each participant’s study therapy, while the randomized groups had different treatment sequences. The comparison is therefore not simply a contrast between ongoing active therapy and ongoing placebo at a shared endpoint time. Understanding the sequence is necessary before assigning a meaning to the arm labels or the estimated contrast.

It also illustrates the difference between an absolute response level and a treatment-group comparison. The arm-level percentages describe the observed share meeting the response definition. The risk difference addresses whether those shares differ between arms. The brief summary states a further question against a reference rate of 40%, but the registry does not report a formal test for that hypothesis. Treating these questions as interchangeable would overstate what the posted analysis establishes.

Precision is as important as the point estimates. The confidence intervals show appreciable uncertainty, particularly for the arm with fewer participants in the primary analysis. The risk-difference interval spans values on both sides of zero, making it inappropriate to read the point estimate alone as a settled comparison. A non-significant result does not demonstrate that meaningful differences are absent.

Finally, the registry record distinguishes posted outcomes from important methodological details that are not reported, including the original sample-size justification, multiplicity plan, missing-data methods, and interim analyses. Recognizing those gaps is part of responsible interpretation. It prevents planning illustrations or descriptive estimates from being mistaken for the trial’s prespecified inferential strategy.

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 primary analysis population is not the same as the total enrollment, and the registry record does not provide a complete participant flow or a full explanation of exclusions and missing outcome data. The Full Analysis Set excludes treated participants who discontinued for reasons unrelated to the treatment regimen or HCV response, but the number excluded for each reason is not reported. The handling of missing RNA measurements is also not reported in the registry record.

The treatment sequence limits a simple interpretation of the randomized contrast. The deferred group received placebo during the first 12-week period and then began open-label combination treatment. The primary endpoint was defined after completion of study therapy. Thus, the posted arm comparison is not a comparison of combination treatment against a control group that remained untreated through the endpoint assessment. The registry record does not provide enough detail to reconstruct all timing and analysis decisions for each participant.

The registry does not report the original sample-size rationale, the detailed statistical analysis plan, the method used to construct the posted confidence intervals, or the multiplicity strategy. It also does not report interim analyses or sensitivity analyses for missing data. Those omissions limit the ability to evaluate prespecification and robustness beyond the posted estimates.

The analysis denominators are unequal, and the smaller deferred-treatment denominator contributes less information to its arm-specific estimate. The population was specific to chronic HCV genotypes 1, 4, or 6 with inherited blood disorders, with and without HIV co-infection; generalization beyond that population requires caution. The safety summary distinguishes the deferred arm’s placebo phase, and does not furnish a complete comparative safety account across all treatment periods. Death counts are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Grazoprevir (MK-5172) and Elbasvir (MK-8742) Combination for Chronic Hepatitis C Virus (HCV) Genotypes 1, 4, and 6 (MK-5172-065) — NCT02252016.
• Registry record last updated 2018-10-03; status last verified 2018-09.
• Results first posted 2017-01-19.
• 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

The registry record describes a completed, randomized, double-blind, parallel-group phase III trial of grazoprevir plus elbasvir in participants with chronic HCV genotypes 1, 4, or 6 and inherited blood disorders. A total of 159 participants were enrolled. The primary endpoint was SVR12, with SVR24 listed as a secondary outcome.

For SVR12, the reported percentages were 93.5% in the immediate-treatment arm and 91.8% in the deferred-treatment arm. The posted risk difference was -0.016, with a 95% confidence interval from -0.106 to 0.074 and an unadjusted p-value of 0.714. The interval includes zero, and the registry does not report a formal test of the primary hypothesis against the reference rate of 40%.

The treatment sequence, analysis-population definition, and uncertainty intervals are central to interpretation. Important details—including the original sample-size justification, missing-data methods, and multiplicity plan—are not reported in the registry record.