A Study to Evaluate the Efficacy and Safety of ABT-493/ABT-530 in Japanese Adults With Genotype 2 Chronic Hepatitis C Virus Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of ABT-493/ABT-530 in Japanese Adults With Genotype 2 Chronic Hepatitis C Virus Infection (NCT02723084), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response 12 Weeks Post-treatment (SVR12): Non-inferiority of Arm A to Arm B.

2. Clinical Question

The primary endpoint was sustained virologic response 12 weeks after the last actual dose of study drug. The registry defines this as plasma HCV RNA below the lower limit of quantification at that time. The posted arm percentages were 97.8% for Arm A and 93.5% for Arm B. The registry’s primary analysis is explicitly a non-inferiority analysis, so the intended statistical question is whether the data rule out a loss in response greater than the prespecified margin, not whether the regimens are identical.

3. Trial Design

This was a phase 3, randomized, open-label, active-comparator, multicenter study with parallel groups. It enrolled 136 participants and is listed as completed. The registry records a start date of 2016-04-08 and a primary completion date of 2017-01-19. The sponsor was AbbVie. The registry’s study title identifies the population as Japanese adults with genotype 2 chronic hepatitis C virus infection.

Random allocation assigns participants to treatment groups by chance, which is intended to make the groups comparable on average at the point of assignment. The open-label design means masking was absent: participants and study personnel were not blinded to the assigned regimens. The active comparator permits a direct comparison with sofosbuvir plus ribavirin, while the parallel design means participants were assigned to one arm rather than receiving both regimens in sequence.

Arm A received co-formulated ABT-493/ABT-530, 300 mg/120 mg once daily for 8 weeks. Arm B received sofosbuvir, 400 mg once daily, with weight-based ribavirin, 600-1000 mg divided twice daily, for 12 weeks. The arm descriptions restrict both groups to genotype 2 infection, direct-acting antiviral treatment-naïve participants, and absence of cirrhosis. The registry’s brief summary describes the purpose as evaluating efficacy and safety of ABT-493/ABT-530 in comparison with sofosbuvir plus ribavirin for 12 weeks.

The reported primary analysis used the intent-to-treat population, defined as all participants who received at least 1 dose of study drug. Missing data after backwards imputation were treated as nonresponse. The registry does not report the original sample-size justification, the randomization procedure in further detail, or the specific statistical methods used for the sponsor’s primary comparison. Those details should not be inferred from the group sizes or the reported endpoint.

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: Intent-to-treat population: all participants who received at least 1 dose of study drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population: all participants who received at least 1 dose of study drug; participants with missing data after backwards imputation were imputed as nonresponders.

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 participants who received at least 1 dose of study drug (ITT population).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Sustained Virologic Response 12 Weeks Post-treatment (SVR12): Non-inferiority of Arm A to Arm B, measured over 12 weeks after the last actual dose of study drug.

The primary endpoint was the percentage of participants with sustained virologic response 12 weeks after the last actual dose of study drug. The registry defines response as a plasma HCV RNA level below the lower limit of quantification at that follow-up time. The endpoint is binary for each participant: the response criterion is either met or not met under the stated definition. Summarizing those participant-level outcomes as a percentage makes the response frequency comparable between randomized groups.

In general, a sustained response endpoint assesses whether the measured virus level remains below the specified threshold after treatment has ended, rather than only while treatment is being taken. The follow-up point is part of the endpoint definition; a response measured at another time would not be the same outcome. Here, the registry specifies assessment 12 weeks after the last actual dose, and its primary efficacy question is non-inferiority of the 8-week Arm A regimen to the 12-week Arm B regimen.

Non-inferiority is used when the question is whether a regimen can be considered not unacceptably worse than an active comparator by a prespecified amount. The registry states a margin of 10%. The margin therefore matters to interpretation: a confidence interval for the between-arm effect must be considered in relation to that allowable loss, rather than using a conventional test of whether the groups differ. The posted arm percentages alone do not convey the uncertainty around the comparison; the reported non-inferiority estimate and interval are needed for that assessment.

The primary population includes participants who received at least 1 dose, and the registry says missing response data after backwards imputation were counted as nonresponse. This rule makes missing endpoint information part of the response classification used in the analysis. It is distinct from assuming that missing participants had a response, and it should be kept in mind when reading the arm percentages and primary comparison.

7. Results Posted in the Registry

• Arm B: 93.5% (43/46) versus 97.8% (88/90) on control; risk difference -4.3 percentage points (95% CI -12.1 to 3.5), risk ratio 0.96 (0.88–1.04); unadjusted two-proportion z-test p = 0.207.

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 Post-Treatment Relapse

• 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:
  • Arm B: 4.4% (2/45) versus 0.0% (0/89) on control; risk difference 4.4 percentage points (95% CI -1.6 to 10.5); unadjusted two-proportion z-test p = 0.045.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary outcomes: sustained virologic response in Arm A, on-treatment virologic failure, and post-treatment relapse. Detailed numerical results in the posted secondary results are available for post-treatment relapse. The record does not report numerical results for the other listed secondary outcomes in the outcome data, so their direction and magnitude should not be inferred.

Across the primary and secondary outcomes, the overall interpretation should distinguish sustained response after treatment from events during treatment or after treatment. The primary endpoint concerns sustained virologic response 12 weeks after the last actual dose. Post-treatment relapse concerns the period from the end of treatment through 12 weeks after the last dose. These outcomes are related to the treatment course but are not interchangeable: they use different event definitions and can have different analysis populations.

The relapse result is based on smaller endpoint-specific denominators than the primary endpoint, and its between-arm estimate is correspondingly uncertain. It can add descriptive context to the primary response comparison, but it does not replace the primary non-inferiority analysis. Nor should a secondary outcome be used alone to reinterpret the primary endpoint, particularly when the registry does not provide a multiplicity strategy for the set of secondary outcomes.

In general, multiple outcomes create multiple opportunities for apparently notable findings to arise by chance. If each is examined without adjustment or a prespecified hierarchy, isolated unadjusted results carry less weight than a single prespecified primary analysis. The registry lists one analysis for the primary endpoint and identifies the primary objective, but it does not report how multiplicity across secondary outcomes was handled. The unadjusted secondary results should therefore be treated as exploratory or supportive evidence, not as independent confirmation of the primary non-inferiority conclusion.

The record gives a secondary outcome name for on-treatment virologic failure and identifies post-treatment relapse, but it does not report numerical values for every listed secondary endpoint. Absence of a posted numerical result is not evidence that no events occurred. A reader should distinguish an outcome that was listed from an outcome for which results are recorded.

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

• Percentage of Participants in Arm A With Sustained Virologic Response 12 Weeks Post-treatment (SVR12)
• Percentage of Participants With With On-treatment Virologic Failure
• Percentage of Participants With Post-Treatment Relapse

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the sustained virologic response definition or did not. The arm-level percentage is the number meeting that definition relative to the analyzed group size. In general, binary outcomes are often compared using a difference in response proportions, a ratio of proportions, or an odds ratio. Each measure uses a different scale. A risk difference is an absolute contrast between percentages, while ratios describe a relative contrast. The registry’s sponsor-reported primary analysis is a risk difference; the additional recalculation includes other unadjusted measures, which should not be mistaken for the sponsor’s reported analysis.

What does non-inferiority ask?

In general, a non-inferiority analysis evaluates whether a new regimen is not worse than an active comparator by more than a prespecified margin. The margin must be set before interpreting the results because it defines what degree of loss the analysis is designed to rule out. The registry states a 10% margin for the comparison of Arm A with Arm B. The confidence interval for the treatment contrast is therefore interpreted against that margin. A conventional test of equality is not interchangeable with this assessment: failing to detect a difference does not, on its own, demonstrate non-inferiority.

The sponsor reports a risk difference of 4.3 with a 95% confidence interval from -3.5 to 12.1. The direction and sign convention matter when reading any difference. The sponsor’s displayed estimate is consistent with comparing Arm A against Arm B, whereas the unadjusted recalculation is expressed as Arm B relative to Arm A. The signs should not be compared without accounting for this reversed orientation. For the sponsor’s stated non-inferiority question, the reported interval is assessed using the sponsor’s direction and the prespecified margin.

What does a confidence interval convey?

In general, a confidence interval gives a range of effect values compatible with the data and the method used to construct the interval. It communicates uncertainty more directly than a point estimate alone. A narrow interval indicates greater precision for that particular estimate, while a wide interval indicates that a broader range of values remains compatible with the data. An interval does not assign a probability to each possible value, and it does not guarantee that the true effect is inside its endpoints.

The unadjusted recalculation reports a risk difference of -0.043 for Arm B relative to Arm A, with an interval from -0.121 to 0.035. That recalculation is based on the posted counts and is not the same as the sponsor’s analysis. The registry also reports an unadjusted p-value of 0.207 for that recalculation. In general, a p-value summarizes how surprising data at least as inconsistent with a null hypothesis would be under a specified model if that null hypothesis were true. It does not measure the probability that the null is true, and it does not quantify the clinical importance of an effect. Here, the recalculated p-value is not the non-inferiority test.

Why can analysis methods differ?

General statistical methods can produce different estimates or intervals from the same study when they use different definitions, models, adjustments, or procedures for uncertainty. Even an unadjusted calculation based on posted counts may not reproduce a sponsor’s analysis if the sponsor used a different method or analysis population. The registry does not identify the sponsor’s specific method in the reported analysis field. Therefore, the sponsor’s result should be read as the reported primary analysis, and the recalculation should be treated as an additional unadjusted description rather than a correction.

Randomization supports comparisons between groups by reducing systematic differences at assignment, but it does not ensure that every observed characteristic is balanced, particularly in a finite study. An unadjusted comparison summarizes the outcome without controlling for other variables. Adjusted analyses can account for selected factors, but the registry does not report such a model for the primary result. No adjustment variables or model should be assumed.

Why does over-dispersion matter?

General explanation: for a binary outcome, the basic binomial model assumes that each participant contributes a response or nonresponse according to a common probability within a group, conditional on the model. Over-dispersion means that variation is greater than that model allows. If present but ignored, standard errors may be too small and confidence intervals too narrow. The registry does not report an over-dispersion assessment or a model requiring such an adjustment. It would therefore be inappropriate to claim that over-dispersion was found or addressed in this trial.

Finally, the primary population and missing-data rule are part of the method, not incidental details. The registry defines the intent-to-treat population as participants who received at least 1 dose and classifies missing data after backwards imputation as nonresponse. This rule affects how incomplete endpoint records contribute to the estimated response percentage. The registry does not report further missing-data counts or sensitivity analyses, so no alternative missing-data result can be inferred.

11. Confidence Intervals and Precision

The sponsor-reported risk difference is 4.3, with a 95% confidence interval from -3.5 to 12.1. That interval is the uncertainty statement accompanying the sponsor’s primary non-inferiority estimate. In general, the point estimate gives one summary of the observed contrast, while the confidence interval shows how much uncertainty remains under the analysis method. The interval should be assessed against the stated non-inferiority margin and the sponsor’s sign convention, rather than judged only by whether it includes zero.

The unadjusted recalculation uses Arm B relative to Arm A and reports a risk difference of -0.043, with a 95% confidence interval from -0.121 to 0.035. The interval includes values on both sides of zero, so the recalculation does not give a sharply determined direction for the unadjusted difference. Its endpoints also allow a range of possible effect sizes. The recalculated estimate is not interchangeable with the sponsor’s primary estimate, because the direction and analysis differ.

In general, an interval’s precision is influenced by the amount of information in the data and by the method used to estimate uncertainty. The primary comparison includes 90 participants in Arm A and 46 in Arm B. The smaller comparator group contributes less information than an equally sized group would, all else equal; the registry does not report the original sample-size justification or intended precision. The observed percentages alone cannot show how precisely the between-group effect is estimated.

Confidence intervals are not predictions of the range of individual participant outcomes. They describe uncertainty in an estimated group contrast under a statistical procedure. They also do not address every source of uncertainty, including limitations in the recorded population, missing data, endpoint definitions, or possible differences in how outcomes are measured. The registry’s reported interval is therefore best interpreted alongside the population definition, missing-data rule, non-inferiority margin, and the stated direction of comparison.

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 figures are illustrative calculations based on the observed effect, not the trial’s own original design assumptions. The registry does not report the original sample-size justification. For this binary outcome, the figures are participants per arm, not total events. The planning assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect.

The rows describe planning for 100%, 75%, and 50% of the observed effect. For the 100% effect, the illustration gives 354 participants per arm for 80% power and 474 participants per arm for 90% power. For 75% of the observed effect, it gives 556 participants per arm for 80% power and 744 participants per arm for 90% power. For 50% of the observed effect, it gives 1,082 participants per arm for 80% power and 1,448 participants per arm for 90% power.

In general, power is the probability that a planned statistical test will detect an effect of the size assumed, under the model and assumptions used for the calculation. The 80% column describes the illustrated group size associated with 80% power under those assumptions; the 90% column describes the size associated with 90% power. Greater power generally requires more participants if the other assumptions stay the same. Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants, as reflected by the larger figures in the smaller-effect rows.

These figures are not observed power. They are planning illustrations using the observed effect as a starting point, and the trial’s original design rationale is not reported in the registry record. They should not be read as the study’s actual planned enrollment or as evidence that the completed trial had the illustrated power.

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 = 0.978; treatment proportion p₁ = 0.935; average p̄ = 0.956.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2892 = 0.5668.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2876 = 0.2420.
4. n = (0.5668 + 0.2420)² / (-0.0430)² = 353.8, rounded up to 354 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 <- 0.977777777777778                          # control proportion
p1 <- 0.934782608695652                          # 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(2723084)
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 = 354 (80% power), 474 (90% power)
 75% of observed effect: n per arm = 556 (80% power), 744 (90% power)
 50% of observed effect: n per arm = 1,082 (80% power), 1,448 (90% power)
power.prop.test: 353.8 
Simulated power at n = 354 per arm: 0.823 (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 sponsor’s own primary analysis is the non-inferiority analysis reported in the registry: a risk difference of 4.3 with a 95% confidence interval from -3.5 to 12.1. The registry states that the comparison was intended to assess non-inferiority of Arm A to Arm B using a 10% margin. That reported result is the primary reference for the trial’s stated question.

The additional re-calculation is a simple unadjusted comparison from the posted summary counts. It expresses the risk difference in the opposite direction, Arm B relative to Arm A, and reports -0.043 with a 95% confidence interval from -0.121 to 0.035. The recalculation is useful as a transparent check on the summary proportions, but it is not a substitute for the sponsor’s non-inferiority analysis. The recalculated unadjusted p-value of 0.207 tests a different null question and should not be read as the sponsor’s non-inferiority result.

The two estimates should be interpreted with their orientations and methods in view. Reversing the comparison reverses the sign, and differences in the analysis method can also affect estimates and intervals. The registry does not report the specific method for the sponsor analysis, so a detailed methodological reconciliation is not possible from the record. The sponsor’s reported result remains the relevant analysis for the stated primary objective; the unadjusted calculation is supplementary context, not a correction to that result.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies sustained virologic response 12 weeks after the last dose as the primary efficacy endpoint and states that the primary question is non-inferiority with a 10% margin. It also lists three secondary outcomes. The registry record does not report a multiplicity adjustment, a testing hierarchy across the secondary outcomes, or whether any secondary analyses were designated as confirmatory. In general, testing several outcomes without a plan to account for multiplicity increases the chance that at least one result appears noteworthy by chance. Consequently, unadjusted secondary findings should be interpreted with caution and should not be given the same confirmatory weight as a prespecified primary analysis.

The primary population is defined as all participants who received at least 1 dose of study drug. The registry says that participants with missing data after backwards imputation were imputed as nonresponders. This provides an explicit rule for missing primary endpoint information, but the registry record does not report how many participants had missing data, why data were missing, or what results would have been obtained under alternative missing-data assumptions. The effect of missingness on the estimates cannot be assessed from the listed rule alone.

In general, a missing-data rule can influence an outcome percentage, especially when the proportion or pattern of missing observations differs between groups. Counting missing participants as nonresponders is one defined approach; it does not demonstrate that missing outcomes truly represented failure. Sensitivity analyses can explore how conclusions change under alternative assumptions, but the registry record does not report such analyses for the primary endpoint.

The record also does not report the sponsor’s detailed statistical model, any adjustment variables, or an original sample-size justification. These omissions limit the ability to reproduce the sponsor’s analysis or evaluate its design assumptions. They should not be filled in by inference from the endpoint, group sizes, or reported estimate. The posted primary result can be described as recorded, while the unadjusted recalculation remains a separate analysis with its own limitations.

16. Safety Results

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

Deaths

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: pneumonia (2.2%), castleman's disease (2.2%), angina unstable (1.1%), pneumothorax spontaneous (1.1%).

The registry reports serious adverse events in 2 of 90 participants in Arm A and 2 of 46 participants in Arm B. It reports 20 participants with other adverse events in Arm A and 26 in Arm B. The listed death count is 0 in each arm. These are counts in the groups at risk as recorded for the safety results; they are not a complete description of every possible safety outcome or its timing.

The serious adverse event terms listed among the top terms include pneumonia at 2.2%, Castleman's disease at 2.2%, unstable angina at 1.1%, and spontaneous pneumothorax at 1.1%. The record does not provide further detail about severity, duration, relationship to study drug, or individual clinical circumstances in these summary figures. A term appearing in the list should be read as a recorded event category, not as proof of cause.

In general, safety counts should be interpreted in the context of group size, follow-up, event definitions, and ascertainment. The arm sizes differ, and raw counts alone do not quantify comparative risk precisely. The registry’s serious-event and other-event totals are descriptive; they do not establish that the regimens have identical safety profiles or that an event was caused by treatment. The record does not report a formal comparative safety analysis in the registry record.

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

The registry reports high sustained virologic response percentages in both randomized groups: 97.8% in Arm A and 93.5% in Arm B. Its primary objective was not a conventional test for equality, but a non-inferiority comparison of the 8-week ABT-493/ABT-530 regimen with the 12-week sofosbuvir and ribavirin regimen using a 10% margin. The sponsor-reported risk difference and confidence interval are the appropriate posted results for that stated objective.

The result does not establish that the regimens are identical. Non-inferiority is a specific statistical conclusion tied to a prespecified margin and an analysis method; it is not proof of equal effects. The separate unadjusted re-calculation is not a substitute for that analysis, and its p-value does not answer the non-inferiority question. The confidence interval also matters: it conveys uncertainty around the estimated contrast, rather than a single definitive effect size.

The findings apply to the population and conditions described in the registry: Japanese adults with genotype 2 chronic hepatitis C virus infection, who were direct-acting antiviral treatment-naïve and without cirrhosis according to the arm descriptions. The endpoint was measured 12 weeks after the last actual dose, and missing data after backwards imputation were counted as nonresponse. The results do not directly answer questions about other populations, other treatment histories, cirrhosis, other genotypes, different follow-up times, or outcomes not reported in the registry.

The safety figures are also limited to the recorded event counts and categories. They do not provide a complete evaluation of comparative safety, establish causation, or describe every aspect of the participants’ experience. The record’s lack of further detail on missing data, methods, and some secondary outcomes limits what can be concluded beyond the posted results.

In general, statistical evidence describes uncertainty in group-level results and does not determine what is appropriate for an individual. These findings should be read as evidence about the trial’s defined population, regimens, endpoint, and analysis, not as medical advice or a universal conclusion about treatment.

18. Why This Trial Matters Statistically

This trial raises a statistically distinct question from whether two treatments differ. Its primary objective was non-inferiority: whether the response with an 8-week regimen could be shown not to fall unacceptably below the response with an active 12-week comparator. This distinction matters because the interpretation depends on the prespecified margin and the confidence interval, not simply on whether a conventional difference test is statistically significant.

The contrast also illustrates why sign conventions deserve attention. The sponsor-reported risk difference and the unadjusted recalculation are expressed in opposite directions. A reader who overlooks that orientation could misunderstand which arm a positive or negative estimate favors. Keeping the estimand, arm order, margin, and interval together is essential to reading a non-inferiority result accurately.

The randomized, parallel-group, active-comparator design supports a direct group comparison, while the open-label nature and unequal group sizes remain relevant context. The endpoint is a defined binary response at a specified follow-up time, and the handling of missing observations is explicitly part of its interpretation. These features make the result more than a comparison of two percentages: it is an estimate subject to a population definition, an outcome rule, a missing-data rule, and a particular non-inferiority framework.

The trial also shows why recalculations from summary counts can be informative but should remain distinct from the sponsor analysis. Such a calculation can offer a transparent view of the crude comparison, yet it may answer a different question or use a different procedure. The registry does not provide enough detail to reconstruct the sponsor’s method, so the primary reported analysis and the supplementary unadjusted estimate should not be conflated.

Finally, the secondary outcomes and safety counts add context but do not automatically strengthen the primary conclusion. Their interpretation depends on completeness of reporting, precision, and multiplicity. The registry’s limitations are therefore part of the statistical reading, rather than footnotes to be ignored.

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 registry record does not report the original sample-size justification or the assumptions used when the trial was designed. The planning figures associated with the observed effect are illustrations and cannot be used to reconstruct the trial’s intended power or enrollment target. The record also does not identify the sponsor’s detailed statistical method for the primary risk difference, limiting independent reproduction of the reported non-inferiority analysis.

The primary analysis population and missing-data rule are stated, but the number of participants with missing endpoint data and the reasons for missingness are not reported in the registry record. No sensitivity analyses for alternative missing-data assumptions are reported in the registry record for this analysis. The impact of missing observations on the result therefore cannot be evaluated from the stated rule alone.

The randomized groups were unequal in size, with 90 participants in Arm A and 46 in Arm B. The comparator estimate is consequently based on fewer participants. This does not invalidate the randomized comparison, but it is relevant when considering precision. The registry does not report detailed baseline characteristics here, so balance on individual prognostic factors cannot be assessed from the recorded details.

The study was open-label, with masking listed as none. The primary endpoint is a laboratory-defined response, but the registry record does not provide further information about outcome assessment procedures or whether any assessment was blinded. The arm descriptions specify a selected population: genotype 2 infection, direct-acting antiviral treatment-naïve participants, and no cirrhosis. The results should not be generalized beyond that population without additional evidence.

The registry lists secondary outcomes, but numerical results are not reported for every listed secondary endpoint in the registry record. It does not report a multiplicity strategy or detailed comparative safety analysis. Serious adverse event counts and selected terms provide limited descriptive information; event attribution, timing, and fuller safety context are not reported. These record-specific gaps restrict broader interpretation and should not be filled by assumptions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of ABT-493/ABT-530 in Japanese Adults With Genotype 2 Chronic Hepatitis C Virus Infection — NCT02723084.
• Registry record last updated 2021-07-16; status last verified 2021-07.
• Results first posted 2019-02-15.
• 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

NCT02723084 is a completed phase 3 randomized, open-label, active-comparator, multicenter parallel study sponsored by AbbVie. It enrolled 136 Japanese adults with genotype 2 chronic hepatitis C virus infection. Arm A received ABT-493/ABT-530 for 8 weeks; Arm B received sofosbuvir plus ribavirin for 12 weeks.

The primary endpoint was sustained virologic response 12 weeks after the last actual dose, with non-inferiority of Arm A to Arm B assessed using a 10% margin. The sponsor-reported risk difference was 4.3, with a 95% confidence interval from -3.5 to 12.1. An unadjusted recalculation from posted counts is a separate estimate and should not be substituted for the sponsor’s primary analysis.

The registry states that the primary population included participants who received at least 1 dose and that missing data after backwards imputation were counted as nonresponse. It reports serious adverse events in 2 participants in each arm and 0 deaths in each arm. The original sample-size justification, detailed sponsor analysis method, and multiplicity handling are not reported in the registry record.