A Study to Evaluate Chronic Hepatitis C Infection in Adults With Genotype 1a Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate Chronic Hepatitis C Infection in Adults With Genotype 1a Infection (NCT01833533), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response 12 Weeks After Treatment; Primary Analyses.

2. Clinical Question

3. Trial Design

PEARL-IV was a completed phase 3 randomized, double-blind, parallel-group study sponsored by AbbVie. The registry lists an enrollment of 305. Its stated purpose was to evaluate the safety and antiviral activity of ABT-450/ritonavir/ABT-267 and ABT-333, with and without ribavirin, in adults with genotype 1a chronic hepatitis C infection without cirrhosis who had not previously received treatment.

Both arms received ABT-450/r/ABT-267 and ABT-333 for 12 weeks. The distinguishing treatment was ribavirin versus placebo ribavirin. The ribavirin arm received weight-based ribavirin, dosed at 1,000 or 1,200 mg daily in divided doses. The other arm received placebo ribavirin twice daily. The registry identifies the study as randomized and double-blind but does not report further details about the randomization procedure, allocation concealment, or which roles were masked.

The primary outcome was sustained virologic response 12 weeks after the last dose of study drug, defined by plasma HCV RNA below the assay’s lower limit of quantitation. The assay LLOQ was 25 IU/mL. The registered primary efficacy objective was framed as noninferiority of each active-treatment arm against a historical control rate, rather than solely as a direct test of the two randomized groups against each other. The registry record does not report the historical control rate, noninferiority margin, sample-size justification, or the trial’s original statistical analysis plan.

The posted primary outcome population was described as all randomized participants who received at least one dose. The randomized group sizes reported for the primary endpoint were 100 and 205. Missing primary endpoint observations were counted as non-responders. The registry’s results also include secondary outcomes related to hemoglobin, sustained response, virologic failure, and relapse; not all listed secondary outcomes have a posted result.

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: All randomized participants who received at least 1 dose of study drug (intent-to-treat \[ITT\] population); participants with missing data were counted as non-responders.

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 After Treatment; Primary Analyses, measured over 12 weeks after last dose of study drug.

The primary endpoint measures the percentage of participants whose plasma HCV RNA was below the assay’s lower limit of quantitation 12 weeks after their final study-drug dose. The assay threshold was 25 IU/mL. This is a binary outcome: each participant is classified as having achieved or not achieved the defined response for the endpoint.

A sustained response measured after treatment is used to assess whether viral RNA remains below the assay threshold after study drugs have stopped, rather than only during dosing. The endpoint is therefore tied to a specified post-treatment follow-up time and a laboratory measurement. It does not, by itself, describe every aspect of participants’ health or long-term outcomes.

The registry states that the primary efficacy endpoints were noninferiority of the response percentage in each treatment arm compared with a historical control rate for noncirrhotic, treatment-naïve participants with genotype 1a infection who received telaprevir and peginterferon/ribavirin. That benchmark differs from the randomized comparison between the two PEARL-IV arms. The registry record does not report the historical rate, the noninferiority margin, or the formal decision criterion, so the posted percentages alone do not establish whether the prespecified noninferiority objective was met.

For the primary population, participants with missing data were counted as non-responders. This rule treats missing endpoint data as not meeting the response definition in the primary analysis. The registry does not report the number of participants with missing endpoint data or additional analyses exploring alternative handling of missing values.

7. Results Posted in the Registry

• ABT-450/r/ABT-267 and ABT-333, Plus RBV: 97.0% (97/100) versus 90.2% (185/205) on control; risk difference 6.8 percentage points (95% CI 1.5 to 12.0), risk ratio 1.07 (1.02–1.14); unadjusted two-proportion z-test p = 0.036.

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 Hemoglobin Decrease to Below the Lower Limit of Normal (LLN) At End of Treatment

• 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:
  • ABT-450/r/ABT-267 and ABT-333, Plus RBV: 42.0% (42/100) versus 3.9% (8/203) on control; risk difference 38.1 percentage points (95% CI 28.0 to 48.1), risk ratio 10.66 (5.20–21.83); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for ABT-450/r/ABT-267 and ABT-333, Plus RBV than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Sustained Virologic Response 12 Weeks After Treatment; Secondary Analyses

• 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:
  • ABT-450/r/ABT-267 and ABT-333, Plus RBV: 97.0% (97/100) versus 90.2% (185/205) on control; risk difference 6.8 percentage points (95% CI 1.5 to 12.0), risk ratio 1.07 (1.02–1.14); unadjusted two-proportion z-test p = 0.036.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for ABT-450/r/ABT-267 and ABT-333, Plus RBV than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Virologic Relapse After Treatment

• 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:
  • ABT-450/r/ABT-267 and ABT-333, Plus RBV: 1.0% (1/98) versus 5.2% (10/194) on control; risk difference -4.1 percentage points (95% CI -7.8 to -0.4), risk ratio 0.20 (0.03–1.52); unadjusted two-proportion z-test p = 0.080.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ABT-450/r/ABT-267 and ABT-333, Plus RBV and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add information about treatment response, laboratory changes, and events after treatment, but they do not all address the same question as the primary endpoint. The sustained-response secondary analysis repeats the response measure, while hemoglobin decrease and relapse describe different outcomes. Virologic failure during treatment is listed as a secondary outcome, but a result for it is not reported in the registry record.

Across the posted secondary results, the hemoglobin outcome differs visibly between the treatment groups, while the relapse estimates are based on relatively few events and are less conclusive in the unadjusted comparison. The secondary sustained-response estimates follow the same broad pattern as the primary response results. These outcomes provide context around the primary endpoint but should not be combined into a single measure or treated as interchangeable evidence.

Unadjusted secondary comparisons carry less weight than a prespecified primary analysis because they may be among several outcomes examined. General statistical explanation: if multiple hypotheses are tested without adjustment, some results can appear statistically notable by chance even when there is no underlying effect. The registry does not report a multiplicity-adjustment procedure for these secondary comparisons, so their p-values should be interpreted as individual, unadjusted results rather than as definitive evidence across the full set of outcomes.

The secondary results also have their own analysis populations and timeframes. For example, the relapse outcome is defined over the period between end of treatment and post-treatment follow-up, whereas the hemoglobin outcome is assessed from baseline to the end of treatment. The registry record does not provide a result for every listed secondary outcome, and the posted secondary findings do not supply the historical control benchmark required for the stated primary noninferiority objective.

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

• Percentage of Participants With Hemoglobin Decrease to Below the Lower Limit of Normal (LLN) At End of Treatment
• Percentage of Participants With Sustained Virologic Response 12 Weeks After Treatment; Secondary Analyses
• Percentage of Participants With Virologic Failure During Treatment
• Percentage of Participants With Virologic Relapse After Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does a response percentage represent?

For a binary endpoint, each participant contributes to one of two categories: meeting or not meeting the stated response definition. The arm-level percentage expresses the observed frequency of participants meeting that definition. In this trial, the primary response required plasma HCV RNA below the assay’s lower limit of quantitation 12 weeks after the last study-drug dose. General statistical interpretation: a percentage is an estimate of the response frequency in the population represented by the study participants; it is not a guarantee that every participant will have the same outcome.

What is a risk difference?

The recalculated risk difference is the response proportion in one randomized group minus the response proportion in the comparator group, expressed on the proportion scale. It describes an absolute contrast between those groups. A value of zero would represent equal observed response proportions; values on either side of zero indicate the direction of the contrast according to the stated group ordering. The recalculated estimate is 0.068. It is an unadjusted comparison based on the posted group summaries and is distinct from the study’s stated historical-control noninferiority objective.

What does the confidence interval add?

A confidence interval gives a range of values compatible with the data and the method used to construct it. General statistical explanation: wider intervals indicate less precision, while narrower intervals indicate greater precision, subject to the method’s assumptions. A confidence interval does not give the probability that the specific fixed treatment contrast lies inside the interval. The sponsor-reported arm-level intervals and the recalculated interval for the between-arm contrast concern different quantities, so they should not be treated as interchangeable.

What does a p-value mean in the recalculation?

The unadjusted p-value of 0.036 belongs to the recalculated between-arm comparison. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the test assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry’s sponsor-reported primary entries list arm-level estimates and confidence intervals but no p-value for the historical-control comparison.

How does noninferiority differ from a direct difference test?

For a noninferiority question, the analysis assesses whether an outcome in a treatment group is not worse than a comparator by more than a prespecified margin. That margin is central to interpreting the result. Here, the stated primary objective compared each treatment arm with a historical control rate. The registry record does not report the rate or margin, so the direct recalculated contrast between the randomized arms cannot substitute for that missing benchmark analysis. General statistical explanation: failure to demonstrate a difference in a conventional superiority test would not, by itself, demonstrate noninferiority; the noninferiority margin and its analysis are essential.

Why does the population definition matter?

The primary endpoint population was described as all randomized participants who received at least one dose. Missing outcome data were counted as non-response. This analysis population and missing-data rule determine how participants contribute to the posted percentages. General statistical explanation: changing who is included or how missing outcomes are classified can change an estimated response frequency, so the population and missing-data approach should accompany interpretation of the result. The registry does not report the number with missing primary outcome data or further sensitivity analyses.

What is not specified about the statistical plan?

The registry record does not report the original sample-size justification, the noninferiority margin, or a full statistical analysis plan. It also does not report whether interim analyses were conducted or how any such analyses were handled. These omissions limit reconstruction of the sponsor’s planned inferential procedure. The posted recalculation is an unadjusted comparison from summary statistics, while the sponsor’s reported primary analyses are identified as legacy noninferiority or equivalence analyses and give arm-level estimates with confidence intervals.

Several secondary comparisons and outcomes are also posted. General statistical explanation: when many outcomes or comparisons are examined, the chance of seeing at least one apparently unusual result can increase if each is assessed separately without accounting for multiplicity. No multiplicity adjustment is reported for the secondary outcomes. Their p-values should therefore be read as unadjusted evidence for the individual comparisons, not as a family-wise conclusion across all outcomes.

11. Confidence Intervals and Precision

The sponsor-reported primary estimates include 95% confidence intervals for each arm: 93.7% to 100.0% for the ribavirin group and 86.2% to 94.3% for the placebo-ribavirin group. These intervals describe uncertainty around the arm-level percentages, using the registry’s reported analysis. They are not intervals for the difference between the arms.

The unadjusted recalculation estimates the risk difference as 0.068, with a 95% confidence interval from 0.015 to 0.120. That interval gives the precision of the recalculated direct contrast under its method. It includes a range of possible risk differences and should not be reduced to the point estimate alone. The unadjusted p-value associated with that comparison is 0.036, but a p-value does not show the range or magnitude of plausible effects.

General statistical explanation: precision is affected by the amount of information in the data and by the variability of the outcome. For a binary endpoint, the number of participants and the observed response frequencies contribute to the uncertainty. The primary groups were different in size, with 100 and 205 participants reported, and the confidence intervals make the uncertainty visible rather than implying exact knowledge of the underlying response frequencies.

The interval for the direct randomized contrast does not answer the separate historical-control noninferiority question. The registry record does not report the historical response rate or noninferiority margin needed to interpret that objective. It also does not report additional uncertainty measures for the sponsor’s historical-control analysis. Precision should therefore be assessed for the estimands that are actually reported, without extending those intervals to an unreported 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 illustrations report participants per arm for 80% power and participants per arm for 90% power. They are not total sample sizes and do not report total events. For each listed fraction of the observed effect, the two columns describe the illustrative number of participants in each arm under the stated planning setup.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The planning figures are based on the observed effect rather than on the trial’s original design assumptions; the registry record does not report the trial’s original sample-size justification or design assumptions.

In general, 80% power means that a study designed under the specified assumptions would have an 80% chance of detecting the chosen effect using the specified test, if that effect and assumptions were correct. The 90% column describes the corresponding design target at 90% power. These are prospective planning concepts, not measures of how likely the observed result was to be true. Smaller target effects are harder to distinguish from random variation, so the illustrations require more participants per arm when the target is a smaller fraction of the observed effect.

These planning calculations are not observed power. They are illustrations of sample sizes under the listed assumptions, not a reconstruction of PEARL-IV’s own design process. They also do not establish that the trial was adequately powered for its original historical-control noninferiority objective, for which the registry record does not report the necessary design assumptions or margin.

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 = 0.902; treatment proportion p₁ = 0.970; average p̄ = 0.936.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3456 = 0.6773.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3423 = 0.2881.
4. n = (0.6773 + 0.2881)² / (0.0676)² = 204.2, rounded up to 205 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 <- 0.902439024390244                          # control proportion
p1 <- 0.97                          # 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(1833533)
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 = 205 (80% power), 273 (90% power)
 75% of observed effect: n per arm = 409 (80% power), 547 (90% power)
 50% of observed effect: n per arm = 1,020 (80% power), 1,364 (90% power)
power.prop.test: 204.2 
Simulated power at n = 205 per arm: 0.821 (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-reported primary results give the response percentage and 95% confidence interval for each arm. The registry identifies these entries as legacy noninferiority or equivalence analyses, but the entries do not include a method, p-value, historical control rate, or noninferiority margin. The registry’s stated primary objective was to compare each arm with a historical control, so the arm-level estimates alone do not permit an independent determination of that objective.

The recalculation instead estimates an unadjusted direct contrast between the two randomized groups. It gives a risk difference of 0.068, a 95% confidence interval from 0.015 to 0.120, and an unadjusted p-value of 0.036. This answers a different question from the sponsor’s stated historical-control analysis. It should be read as a supplementary contrast based on posted summary results, not as a replacement for the sponsor’s full analysis.

The registry’s posted arm-level response percentages and confidence intervals are consistent with the values used in the recalculation, and no discrepancy is flagged. The sponsor-reported results remain the relevant record of the sponsor’s analysis; the recalculation adds an unadjusted between-arm perspective but does not recover unreported elements of the original statistical plan.

15. Multiplicity, Missing Data and Analysis Populations

The primary objective is described as noninferiority of each treatment arm against a historical control rate. That wording entails more than estimating the response percentage in each group: interpretation depends on the chosen historical rate, the noninferiority margin, and the analysis method. The registry record does not report the historical rate or margin, so the posted record does not permit reconstruction of the full decision rule or independent confirmation of the noninferiority assessment.

The record describes the primary analysis population as randomized participants who received at least one dose of study drug. Participants with missing primary endpoint data were counted as non-responders. This is an explicit missing-data rule, but the number of missing outcomes and any sensitivity analyses using other assumptions are not reported in the registry record. The rule therefore can be described, while the impact of missingness cannot be assessed from the posted information.

Multiple outcomes are listed, including the primary sustained-response outcome and secondary outcomes concerning hemoglobin, sustained response, virologic failure, and relapse. A secondary virologic failure result is not reported. The registry record does not report a multiplicity-adjustment procedure, a hierarchy for testing secondary outcomes, or how the overall type I error was controlled across the stated primary comparisons. General statistical explanation: testing several hypotheses separately can increase the chance of at least one false-positive result; the interpretation of individual unadjusted p-values should account for that context.

The record does not report whether interim analyses were planned or conducted, nor whether any stopping boundaries or adjustment procedures were used. It also does not report the original sample-size justification or a complete statistical analysis plan. These are unknown from the registry record; their absence from the posted record should not be taken as evidence that a particular procedure was or was not used.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaemia (1.0%), pancreatitis (1.0%), small intestinal obstruction (1.0%), diverticulitis (0.5%).

The registry reports serious adverse events affecting 3 participants in the ribavirin group and 1 participant in the placebo-ribavirin group. The corresponding groups at risk were 100 and 205. These are group counts, not an adjusted comparison, and they should be read alongside the different group sizes. The registry record does not report deaths in the posted safety summary.

The reported counts of participants with other adverse events were 81 and 138, respectively, among 100 and 205 participants at risk. Serious and other adverse event counts describe different categories and should not be conflated. The listed serious adverse event terms include anemia, pancreatitis, small intestinal obstruction, and diverticulitis; the registry gives percentages for these terms, but the displayed terms do not constitute a complete account of every safety event.

General statistical explanation: a count of events or affected participants does not establish that a treatment caused an event. Interpretation also depends on event definitions, follow-up, severity, and the way events were collected. The registry summary does not provide detailed event-level narratives or an adjusted safety comparison. These figures describe the posted safety record and should not be interpreted as proof of causation or as a complete safety profile.

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

The primary result describes the percentage of participants in each randomized group who met the study’s defined sustained virologic response criterion 12 weeks after the last dose. The sponsor reported arm-level estimates and confidence intervals, and an unadjusted recalculation provides a direct contrast between the randomized groups. Together, these results describe the observed outcomes and the uncertainty around selected estimates.

The recalculated direct comparison is not equivalent to the stated primary objective. That objective evaluated each arm against a historical control rate using a noninferiority framework. Because the registry record does not report the historical rate or noninferiority margin, the direct contrast cannot establish whether that objective was met. A confidence interval and p-value for the randomized-arm difference do not supply the missing historical benchmark.

The result also applies to the population and endpoint described in the record: treatment-naïve adults with genotype 1a chronic hepatitis C without cirrhosis, with response defined by an assay threshold at a specified post-treatment time. It does not automatically describe people outside that study population or outcomes not included in the registry results. Missing primary data were counted as non-response, but the number of missing values is not reported.

General statistical explanation: statistical evidence, uncertainty, and clinical importance are related but distinct. A p-value is not a measure of clinical importance, and a confidence interval does not resolve every design or measurement limitation. The posted secondary outcomes and safety counts contribute additional descriptive information, but their interpretation is limited by unadjusted comparisons, differing timeframes, and outcomes for which no result is reported.

These results should be understood as a record of what was measured and reported in this trial, not as medical advice or a complete account of every possible outcome. The registry record does not report long-term follow-up beyond the stated outcome timeframes, and it does not include the full protocol or statistical analysis plan needed to assess every planned analysis.

18. Why This Trial Matters Statistically

PEARL-IV presents a useful statistical distinction between a randomized comparison and a historical-control noninferiority objective. The two randomized groups allow a direct contrast of their observed response percentages. However, the stated primary efficacy question is whether each arm is noninferior to a historical control rate. Those are different estimands and require different information for interpretation.

The record also illustrates why percentages should be read with their denominators and uncertainty. The primary outcome percentages are accompanied by sponsor-reported confidence intervals, while an unadjusted recalculation quantifies the direct contrast and its interval. Keeping these quantities distinct helps prevent an arm-level confidence interval from being mistaken for a confidence interval on the difference.

The missing details matter statistically. Without the historical rate, noninferiority margin, and original analysis plan, readers cannot fully reconstruct the primary decision framework. Likewise, the absence of a reported multiplicity procedure limits the strength of conclusions drawn from individual secondary p-values. A result may be numerically informative while still leaving important design questions unresolved.

Finally, the registry includes a stated missing-data rule for the primary endpoint, which is an essential element of interpretation. Counting missing data as non-response defines how incomplete primary outcomes enter the analysis, even though the number missing is not reported. Together, these features show why statistical reading requires attention not only to estimates, but also to the population, estimand, comparator, analysis plan, and limitations of the record.

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.

A central limitation for interpretation is that the registry’s stated primary objective uses a historical control rate, but the record does not report that rate or the noninferiority margin. The posted arm-level percentages and the recalculated randomized-group contrast cannot fill in those missing elements. The complete protocol and statistical analysis plan are also not reported in the registry record.

The primary analysis population is defined as randomized participants who received at least one dose, and missing endpoint data count as non-response. The registry does not report how many primary outcomes were missing or provide alternative missing-data analyses. It is therefore not possible to assess from the record how sensitive the primary percentages are to different missing-data assumptions.

The sample-size illustrations are based on the observed effect and stated generic planning assumptions, not on documented trial-design assumptions. They should not be used to infer that the original trial was designed around those calculations. The original sample-size justification is not reported in the registry record.

Some secondary outcomes lack posted results, including virologic failure during treatment. The registry does not report a multiplicity-adjustment procedure for the secondary analyses. Safety figures are summarized as counts and percentages without detailed event-level information, and deaths are not reported in the safety summary. These limitations restrict the conclusions that can be drawn about the full outcome and safety profile from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate Chronic Hepatitis C Infection in Adults With Genotype 1a Infection — NCT01833533.
• Registry record last updated 2021-07-12; status last verified 2021-07.
• Results first posted 2015-01-06.
• 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

PEARL-IV was a completed phase 3 randomized, double-blind, parallel-group study in treatment-naïve adults with genotype 1a chronic hepatitis C without cirrhosis. The two groups received ABT-450/r/ABT-267 and ABT-333 for 12 weeks, with either ribavirin or placebo ribavirin.

The primary outcome was sustained virologic response 12 weeks after the last study-drug dose. The sponsor reported arm-level response percentages with 95% confidence intervals; an unadjusted recalculation describes the direct randomized-group contrast. The stated primary objective used a historical control noninferiority comparison, but its benchmark and margin are not reported in the registry record.

Secondary outcomes and safety counts provide additional context, with some secondary results not reported and no multiplicity procedure specified. Missing primary endpoint data were counted as non-response.