Coadministration of ABT-450/Ritonavir/ABT-267 (ABT-450/r/ABT-267) With Ribavirin (RBV) in Adults With Genotype 4 (GT4) Hepatitis C Virus (HCV) in Egypt: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Coadministration of ABT-450/Ritonavir/ABT-267 (ABT-450/r/ABT-267) With Ribavirin (RBV) in Adults With Genotype 4 (GT4) Hepatitis C Virus (HCV) in Egypt (NCT02247401), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response 12 Weeks Post-treatment (SVR12) in Each Treatment Arm.

2. Clinical Question

The clinical question is descriptive as well as comparative. The registry reports the percentage achieving SVR12 within each arm, with a 95% confidence interval. The arms are not identical in participant characteristics or treatment duration: Arm A represents participants without cirrhosis, while Arms B and C represent participants with compensated cirrhosis and differ in duration. Therefore, the arm results should be read in light of those distinctions rather than as a simple comparison of treatment durations in an otherwise uniform population.

The study enrolled adults with genotype 4 infection in Egypt and included both treatment-naive participants and participants previously treated with pegylated interferon and ribavirin. The record describes no placebo or untreated arm. The question answered by the posted results is how often SVR12 was observed in these treatment groups, not whether the regimen is better than another treatment or no treatment.

3. Trial Design

This was a phase 3, randomized, open-label, parallel study sponsored by AbbVie. The registry lists enrollment of 160 and a completed status. The study began on 2014-11-04, with primary completion on 2016-08-01. Masking was none, so the record does not describe a blinded comparison.

All three arms received ABT-450/r/ABT-267 with ribavirin. Arm A received the combination for 12 weeks and included treatment-naive and treatment-experienced participants without cirrhosis. Arm B received the combination for 12 weeks and included treatment-naive and treatment-experienced participants with compensated cirrhosis. Arm C included participants with compensated cirrhosis and used a 24-week course. The description of treatment-experienced participants specifies prior treatment with pegylated interferon and ribavirin.

These design features matter when interpreting arm differences. The contrast between Arms B and C concerns treatment duration among participants described as having compensated cirrhosis, while comparisons with Arm A also involve a difference in cirrhosis status. Although allocation is listed as randomized, the registry record does not report further details about the allocation procedure, such as how participants were assigned to arms or whether assignment was stratified.

The primary outcome was SVR12, assessed 12 weeks after the last dose. The primary population is defined as the intent-to-treat population consisting of participants who received at least 1 dose of study drug. The registry record does not report the original sample-size justification, the planned statistical comparison, or additional design details that would clarify the intended role of each arm in formal hypothesis testing.

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

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Sustained Virologic Response 12 Weeks Post-treatment (SVR12) in Each Treatment Arm, measured over 12 weeks after last dose.

The primary endpoint is the percentage of participants with sustained virologic response 12 weeks after treatment ended. SVR12 was defined as an HCV RNA level < LLOQ 12 weeks after the last dose of study drug. In practical terms, this endpoint records whether the measured viral RNA was below the assay's lower limit of quantification at the specified follow-up time.

SVR12 is used as a virologic endpoint because it captures a response that persists beyond the period of active dosing, rather than only a change measured while participants are taking study drug. It is a binary outcome at the participant level: each person either meets the stated response definition or does not. The reported percentage therefore describes the proportion meeting the endpoint in each arm; it does not convey the size of any individual participant's RNA change.

The endpoint is measured at a common post-treatment landmark, but the treatment courses were not all the same length. The timeframe is 12 weeks after the last dose, so the date of assessment is anchored to each participant's treatment end rather than to a common date from the first dose. The registry defines the endpoint and population, but it does not report how missing RNA measurements or participants without an evaluable follow-up measurement were handled in the analysis.

Results should be understood as the posted arm-specific proportions and their uncertainty. The outcome definition alone does not establish a causal advantage of one arm over another, particularly because the arm descriptions differ in cirrhosis status and duration.

7. Results Posted in the Registry

• Arm B: 96.8% (30/31) versus 94.0% (94/100) on control; risk difference 2.8 percentage points (95% CI -5.0 to 10.5), risk ratio 1.03 (0.95–1.12); unadjusted two-proportion z-test p = 0.548.
• Arm C: 93.1% (27/29) versus 94.0% (94/100) on control; risk difference -0.9 percentage points (95% CI -11.2 to 9.4), risk ratio 0.99 (0.89–1.11); unadjusted two-proportion z-test p = 0.860.

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 On-treatment Virologic Failure in Each Treatment Arm

• 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: 3.2% (1/31) versus 1.0% (1/100) on control; risk difference 2.2 percentage points (95% CI -4.3 to 8.7), risk ratio 3.23 (0.21–50.08); unadjusted two-proportion z-test p = 0.377.
  • Arm C: 3.4% (1/29) versus 1.0% (1/100) on control; risk difference 2.4 percentage points (95% CI -4.5 to 9.4), risk ratio 3.45 (0.22–53.45); unadjusted two-proportion z-test p = 0.347.
• 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 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Post-treatment Relapse Within 12 Weeks Following End of Treatment in Each Arm

• 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: 0.0% (0/30) versus 3.1% (3/98) on control; risk difference -3.1 percentage points (95% CI -6.5 to 0.3); unadjusted two-proportion z-test p = 0.332.
  • Arm C: 0.0% (0/28) versus 3.1% (3/98) on control; risk difference -3.1 percentage points (95% CI -6.5 to 0.3); unadjusted two-proportion z-test p = 0.349.
• 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 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover on-treatment virologic failure and post-treatment relapse. Together, they describe different parts of the response pattern: one concerns virologic failure during treatment, and the other concerns loss of response after treatment has ended. They complement SVR12, but they are not interchangeable with the primary endpoint and do not replace its follow-up definition.

Across the posted secondary results, events were uncommon, and the arm-specific comparisons are based on limited event counts. The resulting estimates are imprecise, as reflected by broad confidence intervals. The overall pattern does not establish a clear separation among the arms or overturn the cautious reading of the primary outcome. The registry lists no reported analyses for these secondary outcomes; the comparisons are unadjusted recalculations rather than a reported confirmatory testing strategy.

Secondary outcomes generally carry less evidential weight when their role in a prespecified hierarchy is not documented, and when multiple endpoints or arm comparisons are considered without a reported multiplicity approach. Repeated testing can increase the chance of finding an apparently notable result by chance. The registry record does not say whether these outcomes were designated for formal hypothesis testing, whether any were prioritized, or how multiplicity was addressed. Consequently, they are best treated as descriptive supporting information, not as independent proof of comparative benefit or harm.

The secondary endpoints also have distinct timeframes and analysis denominators. Those features should be kept in mind when reading the endpoint-specific results. A difference in the observed percentages across endpoints does not, on its own, indicate a contradiction: the outcomes measure different events and use different follow-up periods.

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

• Percentage of Participants With On-treatment Virologic Failure in Each Treatment Arm
• Percentage of Participants With Post-treatment Relapse Within 12 Weeks Following End of Treatment in Each Arm

9. Statistical Interpretation

10. Statistical Methods Explained

What does the endpoint percentage represent?

The primary outcome is binary at the participant level: the SVR12 definition is either met or not met. The arm percentage expresses the share of the analysis population meeting that definition. A percentage is an intuitive way to summarize a binary outcome, but it does not show the underlying pattern of individual measurements or explain why a participant did not meet the endpoint.

The registry reports the number evaluated and the percentage for each arm, with a 95% confidence interval. The primary population is identified as all participants who received at least 1 dose of study drug. The denominators for the primary results are 100.0 for Arm A, 31.0 for Arm B, and 29.0 for Arm C. These are arm-specific analysis counts, not a statement about the handling of participants who may have had missing outcome measurements.

What does a confidence interval communicate?

A confidence interval describes uncertainty around an estimate under the method used to calculate it. A narrower interval indicates greater precision, while a wider interval indicates that the data are compatible with a broader range of underlying values. It is not a range that guarantees where the true value lies, and it does not mean that every value inside the interval is equally plausible.

For the arm-specific percentages, the registry gives 95% confidence intervals. The intervals for Arms B and C are wider than the interval for Arm A, consistent with the smaller reported arm denominators. The interval should be considered alongside the point estimate: reading only the point estimate hides how uncertain it is, while reading only the interval obscures the central observed value.

How should the recalculated comparisons be read?

The comparison statistic is a risk difference, which expresses the difference between two proportions on the proportion scale. The posted comparisons use Arm A as the reference and compare its result with Arm B or Arm C. For Arm B versus Arm A, the reported estimate is 0.028; for Arm C versus Arm A, it is -0.009. These are recalculated unadjusted comparisons based on posted summary statistics. They are not identified as the trial's prespecified analysis.

The confidence interval for a risk difference gives a range of values compatible with the data under the calculation method. If the interval includes zero, the data do not clearly distinguish a positive from a negative difference. Both primary risk-difference intervals include zero. The p-values are also unadjusted. They should not be interpreted as the probability that the arms are equal, or as proof of no difference. The registry record does not report the sponsor's formal comparative analysis or a plan for adjustment.

Why can percentages be uncertain when they look close?

The arm estimates are based on different amounts of information. When fewer participants contribute to an estimate, each outcome can have a stronger influence on the percentage, and uncertainty is often greater. This is especially relevant when the outcome is common and the number of participants who do not meet it is small. A small number of events can make between-arm estimates sensitive to the outcomes of individual participants.

Random allocation is a design feature, not a guarantee that every arm will have identical characteristics or that an observed difference is caused by treatment. In this study, the arm descriptions themselves identify differences in cirrhosis status and duration. The reported results need to be understood within those clinical groupings.

What is not documented about the analysis?

The registry record does not report a detailed statistical analysis plan, the original sample-size justification, handling of missing primary measurements, or whether any interim analyses were planned or conducted. It lists no reported analyses for the primary outcome. The posted recalculations can help describe the summaries, but they cannot fill in the missing information about the planned analysis or replace a sponsor analysis. The discrepancy indicator is false, so no discrepancy with a sponsor analysis is flagged in the record.

11. Confidence Intervals and Precision

The SVR12 confidence intervals are important because the arm percentages are estimates rather than exact descriptions of the underlying response probabilities. Arm A's reported 94.0% has a 95% confidence interval from 87.5% to 97.2%. Arm B's 96.8% has an interval from 83.8% to 99.4%, and Arm C's 93.1% has an interval from 78.0% to 98.1%. The intervals for B and C span a broader range than the interval for A, so their point estimates are less precise.

The risk-difference intervals provide another view of comparative precision. The estimate for Arm B versus Arm A is 0.028, with an interval from -0.050 to 0.105. The estimate for Arm C versus Arm A is -0.009, with an interval from -0.112 to 0.094. Each interval crosses zero, indicating that the posted summary data are compatible with differences in either direction. The intervals also cover values that would represent nontrivial differences, so a lack of clear separation is not evidence that the arms are equivalent.

Confidence intervals do not account for every possible source of uncertainty. Their interpretation depends on the statistical method and assumptions, and the registry record does not report a full analysis plan. They also do not resolve the structural differences among arms: Arm A participants were without cirrhosis, whereas participants in Arms B and C had compensated cirrhosis, and the duration varied between B and C.

The appropriate reading is therefore cautious. The point estimates are similar in appearance, but the uncertainty is substantial for the smaller arm groups and the comparative intervals do not identify a clear difference. Precision is limited for claims about comparative effects, particularly claims that would require demonstrating equivalence or a specific degree of benefit.

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 display translates the observed risk-difference estimates into illustrative sample sizes under the assumptions stated for the calculation. The figures are participants per arm, not total participants and not total events. The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers detecting the stated fraction of that effect.

For the comparison of Arm B with Arm A, planning for 100% of the observed effect gives 897 participants per arm for 80% power and 1,200 participants per arm for 90% power. For the comparison of Arm C with Arm A, the corresponding figures are 11,780 participants per arm for 80% power and 15,770 participants per arm for 90% power. These are planning illustrations based on the recalculated observed effects, not the sample sizes used to conduct this trial. The registry record does not report the trial's original sample-size assumptions or justification.

The 80% power column describes a design that, under the calculation assumptions and if the chosen effect were the true effect, would have an 80% chance of detecting that effect according to the specified testing framework. The 90% column uses a higher target chance of detection, which generally requires more participants. Rows for 75% or 50% of the observed effect represent smaller effects to detect; smaller effects need more participants because they are harder to distinguish from sampling variation.

The curve should be read as a display of how the planning requirement changes as the assumed effect changes, not as a forecast of what this trial would have found under another sample size. The figures are not observed power. They should not be used to infer that the completed trial was adequately or inadequately powered, since the original design assumptions are not reported.

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 = 0.940; treatment proportion p₁ = 0.968; average p̄ = 0.954.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2967 = 0.5814.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2960 = 0.2491.
4. n = (0.5814 + 0.2491)² / (0.0277)² = 896.3, rounded up to 897 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 <- 0.94                          # control proportion
p1 <- 0.967741935483871                          # 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(2247401)
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 = 897 (80% power), 1,200 (90% power)
 75% of observed effect: n per arm = 1,709 (80% power), 2,287 (90% power)
 50% of observed effect: n per arm = 4,099 (80% power), 5,487 (90% power)
power.prop.test: 896.3 
Simulated power at n = 897 per arm: 0.808 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how multiplicity was handled. It identifies a primary endpoint and two secondary outcomes, but does not give a testing hierarchy, an adjustment method, or a family of hypotheses that would define confirmatory comparisons. The posted comparisons are unadjusted recalculations. When several endpoints or arm comparisons are examined, interpreting each unadjusted p-value as though it were the only test can overstate the strength of evidence. Without the planned testing strategy, the secondary results should be considered descriptive.

The record lists no reported analyses for the primary or secondary outcomes. It therefore does not document a sponsor-reported analysis model, adjustment for covariates, or formal handling of the arm structure. The record also does not report whether interim analyses were planned or conducted. These omissions do not change the posted outcome values, but they limit the ability to assess whether the displayed comparisons match the trial's prespecified inferential plan.

The primary population is defined as all participants who received at least 1 dose of study drug. This definition identifies the population used for the primary endpoint, but does not specify how missing RNA measurements were treated, whether participants without follow-up were counted as nonresponders, or what rules were used for other unevaluable outcomes. Those details are not reported in the registry record.

Denominators differ across endpoints. The primary outcome uses denominators of 100.0 for Arm A, 31.0 for Arm B, and 29.0 for Arm C. The relapse outcome uses 98.0, 30.0, and 28.0, respectively. Different denominators can arise from endpoint-specific analysis populations or data availability, but the reason for the differences is not reported in the registry record. The on-treatment failure outcome has its own listed denominators as well.

The record does not report a missing-data sensitivity analysis or a comparison of participants with and without observed outcomes. Without those details, the impact of missing observations on the estimates cannot be assessed from the registry summaries alone. The original statistical plan, including any prespecified assumptions about missingness and analysis populations, is not reported in the registry record.

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: oesophageal varices haemorrhage (3.4%), bile duct stone (3.4%), cholecystitis acute (3.4%), apnoea (1.0%), deep vein thrombosis (1.0%).

The registry reports serious adverse events by arm using the number at risk and the number affected. Arm A had 2 serious adverse events among 100 at risk. Arm B had 0 among 31 at risk. Arm C had 2 among 29 at risk. These are counts within each arm; they do not by themselves establish whether an event was caused by treatment or whether the underlying risks differ between arms.

The listed serious event terms include oesophageal varices haemorrhage, bile duct stone, and acute cholecystitis, each reported as 3.4%, as well as apnoea and deep vein thrombosis, each reported as 1.0%. The record does not provide enough information in these summaries to attribute an event to the study drug, determine its clinical course, or compare the event terms by arm.

Death counts are not reported in the registry record. Serious adverse events are distinct from the broader other-adverse-event counts, which are also listed by arm. These safety summaries are descriptive and should be read alongside the study's participant groups and limited arm sizes, not as a definitive comparative safety analysis.

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

The results show that SVR12 was reported in a high proportion of participants in each arm: 94.0% in Arm A, 96.8% in Arm B, and 93.1% in Arm C. The confidence intervals show that the estimates are uncertain, with wider intervals in Arms B and C. The recalculated unadjusted risk-difference intervals include zero for both comparisons with Arm A, so the posted summaries do not establish a clear difference between those arm results.

This finding is not the same as showing that the arms are equivalent. Equivalence requires a prespecified margin and an analysis designed to determine whether the uncertainty is confined within that margin. Non-inferiority likewise requires a specified margin and an appropriate analysis. Those details are not reported in the registry record. Nor do the summaries establish superiority of one arm.

The arm descriptions also prevent a simple interpretation of every difference as an effect of treatment duration. Arm A included participants without cirrhosis; Arms B and C included participants with compensated cirrhosis. The B-versus-C comparison is between different durations in the described cirrhosis population, while comparisons involving Arm A also differ in cirrhosis status. The record does not report a formal analysis designed to disentangle those factors.

These results should not be read as medical advice or as a guarantee about an individual outcome. They describe the reported trial population and endpoint under the registry definitions. The summaries do not establish how the findings apply to people outside the study population, and they do not provide a comparison with another regimen. The most defensible interpretation is descriptive: SVR12 percentages were high across the three arms, but the comparative estimates are not precise enough to support strong claims of difference or equivalence.

17. Why This Trial Matters Statistically

This trial illustrates why a headline percentage and a comparative conclusion are not the same thing. The arm-specific SVR12 percentages are close, but the confidence intervals and recalculated risk-difference intervals show appreciable uncertainty. In particular, the smaller arm denominators yield less precise estimates. Statistical interpretation must account for that uncertainty rather than treating the observed point estimates as exact.

The trial also makes the importance of the clinical comparison explicit. Randomization is listed, but the arms differ in their described cirrhosis status and treatment duration. This means that the meaning of an arm contrast depends on which groups are being compared. A numerical difference between Arm A and either cirrhosis arm cannot be attributed to duration alone, because the participant groups also differ.

The planning illustration reinforces a general design lesson: sample-size requirements depend on the effect a study aims to detect and on the chosen planning assumptions. Smaller effects require more participants to detect. Such calculations are distinct from the observed results and cannot retrospectively demonstrate that a completed study had adequate power. The registry record does not report the original sample-size justification, making it especially important not to confuse the illustrative planning values with the trial's actual design rationale.

Finally, the absence of reported analyses and multiplicity details limits the strength of inferential claims. Clear endpoint definitions and arm summaries are useful, but readers also need the analysis plan, missing-data rules, and testing strategy to judge how confirmatory the comparisons are. This record is therefore a useful example of interpreting outcome estimates while keeping design, precision, and reporting limitations in view.

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 arm groups are not described as having the same clinical characteristics. Arm A included participants without cirrhosis, while Arms B and C included participants with compensated cirrhosis. Comparisons involving Arm A therefore combine differences in the treatment arm with differences in the described participant group. The registry record does not report a detailed adjusted analysis that could clarify how those differences were handled.

The study included treatment-naive participants and participants previously treated with pegylated interferon and ribavirin. The posted summaries do not separate SVR12 results by prior treatment status, so the overall arm estimates do not show whether outcomes differed across those histories. Likewise, the record does not provide subgroup results by other participant characteristics.

Arm B and Arm C differ in treatment duration, but the summaries are limited in precision, especially for the smaller arms. The registry does not report a formal duration-comparison analysis or a prespecified margin for equivalence or non-inferiority. The posted risk-difference comparisons use Arm A as reference and are unadjusted recalculations, not a documented sponsor analysis.

Other limitations arise from incomplete analysis reporting. The statistical analysis plan, original sample-size rationale, approach to missing outcomes, and multiplicity method are not reported in the registry record. Denominators differ by endpoint, but the reasons are not explained. The record also does not report death counts. These gaps restrict interpretation of both comparative effectiveness and safety from the registry summaries alone.

The study was conducted in adults in Egypt with genotype 4 hepatitis C. The registry results should be understood within that stated population; the summaries do not establish applicability to other populations or settings. These limitations do not negate the posted observations, but they narrow the conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Coadministration of ABT-450/Ritonavir/ABT-267 (ABT-450/r/ABT-267) With Ribavirin (RBV) in Adults With Genotype 4 (GT4) Hepatitis C Virus (HCV) in Egypt — NCT02247401.
• Registry record last updated 2021-07-30; status last verified 2021-07.
• Results first posted 2017-07-27.
• 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

NCT02247401 is a completed phase 3 randomized, open-label, parallel study sponsored by AbbVie. It evaluated ABT-450/r/ABT-267 with ribavirin in adults in Egypt with chronic hepatitis C genotype 4 infection, including treatment-naive and treatment-experienced participants with or without compensated cirrhosis.

The primary endpoint was SVR12, defined by HCV RNA < LLOQ 12 weeks after the last dose. Reported SVR12 was 94.0% in Arm A, 96.8% in Arm B, and 93.1% in Arm C. The unadjusted recalculated comparisons have confidence intervals that include zero; the registry record lists no reported analyses.

Arm descriptions differ by cirrhosis status and treatment duration. The registry record does not report the original sample-size justification, detailed analysis plan, multiplicity approach, or handling of missing outcome data. The posted results are best read as arm-specific descriptive estimates with uncertainty, rather than definitive evidence of superiority or equivalence.