Safety and Efficacy of Boceprevir in Previously Untreated Subjects With Chronic Hepatitis C Genotype 1 (Study P05216AM2) (COMPLETED): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Boceprevir in Previously Untreated Subjects With Chronic Hepatitis C Genotype 1 (Study P05216AM2) (COMPLETED) (NCT00705432), a randomized phase 3 study. The primary outcome is Sustained Virologic Response (SVR) Rate.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, double-masked, parallel-group trial of boceprevir or placebo with PegIntron and ribavirin in previously untreated adults with chronic hepatitis C genotype 1. The registry reports enrollment of 1472 and lists the study status as completed. The recorded start was 2008-08 and primary completion was 2010-05.

The study was organized into two separately described cohorts, Cohort I for White participants and Cohort II for Black participants. Participants in each cohort were assigned among three treatment groups. Each group received PEG plus RBV during a 4-week lead-in. The placebo group then continued PEG and RBV with placebo, while the active groups added boceprevir. One active regimen was labeled 24 Weeks (RGT), and the other 44 Weeks. The registry says participants in the shorter regimen were offered response-guided therapy at treatment week 28, but the detailed criteria are incomplete in the record. The placebo regimen and the 44-week boceprevir regimen include 24 weeks of post-treatment follow-up in their descriptions.

The primary endpoint was assessed at follow-up week 24. The registry identifies the primary analysis population as the full analysis set, consisting of randomized participants who received at least one dose of PEG, RBV, or boceprevir. It also lists secondary outcomes concerning SVR in participants treated with study drug, HCV-RNA at follow-up, and early virologic response. The protocol’s original sample-size assumptions, allocation ratios, detailed masking procedures, and a complete account of treatment discontinuation rules are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 373 participants were screened but not randomized. 1099 participants were randomized. Only 1097 received at least one dose of PegIntron (PEG) + Ribavirin (RBV) (lead-in treatment).

Treatment Period

Reasons for not completing this period:

Follow-up Period (Upto Week 72)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS). All randomized participants who received at least one dose of any study medication (PEG, RBV or boceprevir).

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Sustained Virologic Response (SVR) Rate, measured over At Follow-up Week (FW) 24.

The primary endpoint is the percentage of participants who achieved sustained virologic response at follow-up week 24. The registry defines achievement as undetectable plasma HCV-RNA at that follow-up visit. HCV-RNA was measured with a nucleic acid amplification test whose limit of detection is 9.3 IU/mL. If the week-24 result was missing after an undetectable result at follow-up week 12, the participant was to be counted as having achieved SVR.

SVR is a binary outcome at the participant level: each participant is classified as meeting or not meeting the endpoint under the registry’s definition. Reporting the percentage makes the observed frequency in each treatment group easy to compare. A risk difference expresses the absolute contrast in those percentages, in percentage points when presented on the percentage scale. It does not describe how quickly the response occurred or the amount by which viral RNA changed. Those questions require different outcome measures.

SVR is used in this trial as the principal measure of virologic response after treatment. The primary endpoint alone does not describe adverse events, treatment burden, or outcomes beyond the stated assessment time. Its interpretation also depends on the specified handling of missing week-24 results and the analysis population. The registry describes those elements for the primary endpoint, but details of all other missing-data procedures are not reported in the registry record.

7. Results Posted in the Registry

• Cohort I - 2. Boceprevir + PEG + RBV - 24 Weeks (RGT): 66.8% (211/316) versus 40.2% (125/311) on control; risk difference 26.6 percentage points (95% CI 19.1 to 34.1), risk ratio 1.66 (1.42–1.94); unadjusted two-proportion z-test p = <0.001.
• Cohort I - 3. Boceprevir + PEG + RBV - 44 Weeks: 68.5% (213/311) versus 40.2% (125/311) on control; risk difference 28.3 percentage points (95% CI 20.8 to 35.8), risk ratio 1.70 (1.46–1.99); unadjusted two-proportion z-test p = <0.001.
• Cohort II - 1. Placebo + PEG + RBV: 23.1% (12/52) versus 40.2% (125/311) on control; risk difference -17.1 percentage points (95% CI -29.8 to -4.4), risk ratio 0.57 (0.34–0.96); unadjusted two-proportion z-test p = 0.018.
• Cohort II - 2. Boceprevir + PEG + RBV - 24 Weeks (RGT): 42.3% (22/52) versus 40.2% (125/311) on control; risk difference 2.1 percentage points (95% CI -12.4 to 16.6), risk ratio 1.05 (0.75–1.49); unadjusted two-proportion z-test p = 0.774.

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.

Sustained Virologic Response (SVR) Rate in Participants Treated With Study Drug (Boceprevir or Placebo)

• 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:
  • Cohort I - 2. Boceprevir + PEG + RBV - 24 Weeks (RGT): 69.6% (211/303) versus 42.1% (125/297) on control; risk difference 27.5 percentage points (95% CI 19.9 to 35.2), risk ratio 1.65 (1.42–1.93); unadjusted two-proportion z-test p = <0.001.
  • Cohort I - 3. Boceprevir + PEG + RBV - 44 Weeks: 71.2% (213/299) versus 42.1% (125/297) on control; risk difference 29.1 percentage points (95% CI 21.5 to 36.8), risk ratio 1.69 (1.45–1.97); 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 Cohort I - 2. Boceprevir + PEG + RBV - 24 Weeks (RGT) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cohort I - 3. Boceprevir + PEG + RBV - 44 Weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes that extend beyond the primary SVR assessment. These include SVR among participants treated with study drug, HCV-RNA status at follow-up, and early virologic response at specified treatment visits, including whether early response was followed by SVR. Such outcomes can provide context about response during treatment and at different follow-up times, rather than relying on the primary endpoint alone.

The secondary SVR results posted for Cohort I follow the same broad pattern as the primary results: the boceprevir groups have higher reported SVR percentages than the placebo group. This consistency supports describing the primary pattern as also present in the posted treated-participant summary, while recognizing that the analysis population differs. The treated-participant result is not an independent replication of the primary trial comparison; it draws on participants from the same trial and concerns a related endpoint.

The registry record lists the other follow-up and early-response outcomes, but detailed results for those measures are not reported in the registry record. They therefore cannot be used to make claims about how response developed over time or whether early response predicted later SVR in this study.

Secondary findings generally carry less confirmatory weight than the primary endpoint. There may be multiple outcomes, treatment comparisons, time points, and analysis populations, and the registry does not report a multiplicity adjustment plan. When many results are examined, chance findings become more plausible unless the analysis plan accounts for that multiplicity. Secondary results can still be informative, but their interpretation should consider their relationship to the primary endpoint, their analysis population, and the fact that they are not separate trials. The posted secondary summaries add context; they do not replace the sponsor’s primary analysis or resolve its limitations.

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

• Sustained Virologic Response (SVR) Rate in Participants Treated With Study Drug (Boceprevir or Placebo)
• Number of Participants With Undetectable HCV-RNA at Follow-up Week 12 and at 72 Weeks After Randomization.
• Number of Participants With Early Virologic Response (Undetectable HCV-RNA at Treatment Week 2, 4, 8, 12, 16, or 20)
• Number of Participants With Early Virologic Response (Undetectable HCV-RNA at Treatment Week 4, 8, 12, 16, or 20) Who Achieved SVR

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the observed group results from the uncertainty around them. The primary endpoint is a percentage, because SVR is classified for each participant as either achieved or not achieved. A percentage summarizes the frequency of that binary outcome in a group. The risk difference compares two such frequencies by subtracting one from the other. A positive difference in the boceprevir-versus-placebo comparisons indicates a higher observed SVR percentage in the boceprevir group; a negative difference indicates a lower observed percentage. The difference is an absolute contrast, unlike a risk ratio or odds ratio, which expresses a relative contrast.

What does the sponsor’s test do?

The sponsor reports using the Cochran-Mantel-Haenszel chi-square test for the primary comparisons. In general, this method tests an association between treatment group and a categorical outcome while accounting for specified strata. It can produce a stratified comparison rather than simply comparing the raw percentages as if every participant came from a single unstratified group. The exact stratification variables and full model details are not reported in the registry record. The results should therefore be described using the method the registry names, without assuming details of its implementation that are not stated.

The p-value is a measure of how compatible the data are with a null hypothesis of no difference under the test’s assumptions. A small p-value is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The sponsor-reported p-values describe its analyses. Recalculated p-values are labeled unadjusted because they come from simple comparisons of posted summary statistics and do not reproduce the sponsor’s stratified analysis. The reported and recalculated values may differ for that reason, as well as because of how the summaries are constructed.

How should effect size be distinguished from evidence?

The risk difference gives the absolute size and direction of a comparison. A confidence interval gives a range of values compatible with the data and the method used, subject to the assumptions of that method. The interval conveys uncertainty about the estimate; it is not a range containing a known true value with certainty. If an interval includes no difference, the data are compatible with a range spanning both directions of effect under that interval procedure. If it excludes no difference, that is consistent with a statistically detectable contrast under the procedure, but does not establish clinical importance. The sponsor’s intervals and tests should be interpreted together rather than relying on a threshold alone.

Randomization is intended to support fair comparisons by assigning participants to treatment groups, while masking is intended to reduce the influence of treatment knowledge on study conduct or outcome assessment. The registry lists the study as randomized and double-masked. The record does not describe the precise randomization sequence, concealment process, masking maintenance, or all analysis details. The trial has parallel groups: participants were assigned to a regimen rather than crossing between regimens as part of the described design.

The primary analysis population is the full analysis set, defined in the registry as randomized participants who received at least one dose of any study medication. This definition is narrower than a description of every person randomized, because receipt of at least one dose is part of the stated inclusion rule. The registry also specifies an outcome rule for missing week-24 data after an undetectable result at follow-up week 12. Other missing-data rules, exclusions, and sensitivity analyses are not reported in the registry record. That means the endpoint definition is partly clear, but the robustness of findings to alternative missing-data assumptions cannot be assessed from the record alone.

Finally, there are multiple treatment comparisons and several listed secondary outcomes. Testing several hypotheses can increase the chance of at least one apparently positive result by chance if all are treated as independent opportunities for significance. Whether and how the sponsor controlled multiplicity is not reported in the registry record. This is one reason to distinguish the prespecified primary comparisons, where their status is stated, from secondary or additional analyses and to avoid treating every unadjusted p-value as confirmatory.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence intervals provide a view of the uncertainty around the primary risk differences. For Cohort I, the interval for the response-guided boceprevir regimen compared with placebo is 19.1 to 34.1 percentage points; for the 44-week regimen, it is 20.8 to 35.8 percentage points. Both intervals are above no difference. In Cohort II, the corresponding intervals are 1.6 to 36.9 percentage points and 12.2 to 47.1 percentage points. The first Cohort II interval is much wider in relation to its estimate than the Cohort I intervals, and the second also spans a broad range of possible differences. This indicates less precision in those Cohort II comparisons.

A confidence interval is not a guarantee that the true effect lies within its endpoints. In general, it summarizes the range of estimates reasonably compatible with the observed data under the analysis method and its assumptions. A narrower interval means greater precision for that estimate; a wider interval means more uncertainty. Precision is influenced by the amount of information available and by outcome variability. The Cohort II groups have smaller posted analysis counts than the Cohort I groups, which is consistent with less information contributing to those comparisons, although the registry does not provide a formal analysis of the causes of the differences in precision.

The simple recalculated intervals differ somewhat from the sponsor’s intervals because the methods are not the same. Since the record flags a discrepancy, the sponsor’s own stratified analysis is the primary source for the reported comparison. The intervals should also be considered alongside the endpoint definition, population, and missing-data rules. A statistically detectable estimate can still be imprecise about its magnitude, and statistical precision does not by itself establish clinical importance.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustrations translate an observed risk difference into hypothetical numbers of participants per arm for a future two-group comparison. The entries are not the enrollment targets for this trial. For example, the rows describe planning for 100%, 75%, or 50% of the observed effect. These are scenarios for how the required sample size would change if the effect to detect were smaller than the observed estimate. Smaller effects require more participants to distinguish them from no difference with the same design assumptions.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For these binary outcomes, the figures are participants per arm; they are not total event counts. The trial’s own original design assumptions and sample-size justification are not reported in the registry record. The illustration is therefore not a reconstruction of the protocol’s planning process.

The 80% power column gives the estimated participants per arm for a hypothetical study designed to have an 80% chance of detecting the assumed effect under the stated assumptions, if that effect were present. The 90% power column expresses the corresponding planning target for a higher chance of detection. These are design quantities, not probabilities that the trial’s result is correct and not measures of the strength of evidence in the completed study. The sample-size figures are planning illustrations, not observed power.

Large illustrative sample sizes can arise when the observed difference is small, because a small contrast is harder to distinguish from random variation. In Cohort II, the response-guided comparison has a small recalculated observed difference, and the corresponding planning figures are much larger than those for comparisons with larger observed effects. Such figures are sensitive to the estimated effect used and should not be read as firm requirements for a future trial without a complete design specification.

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 = 0.402; treatment proportion p₁ = 0.668; average p̄ = 0.535.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7054 = 1.3825.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6799 = 0.5722.
4. n = (1.3825 + 0.5722)² / (0.2658)² = 54.1, rounded up to 55 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 <- 0.401929260450161                          # control proportion
p1 <- 0.667721518987342                          # 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(705432)
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 = 55 (80% power), 72 (90% power)
 75% of observed effect: n per arm = 98 (80% power), 131 (90% power)
 50% of observed effect: n per arm = 221 (80% power), 295 (90% power)
power.prop.test: 54.1 
Simulated power at n = 55 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons using the Cochran-Mantel-Haenszel chi-square method. Those analyses compare each boceprevir regimen with placebo within each cohort and include reported differences, 95% confidence intervals, and p-values. The simple recalculations use the posted group summary statistics to estimate unadjusted risk differences and intervals. They do not reproduce the sponsor’s named stratified test.

For Cohort I, the sponsor reports differences of 26.6 and 28.3 percentage points, while the recalculated estimates are 0.266 and 0.283 on a proportion scale. For Cohort II, the sponsor reports differences of 19.2 and 29.7 percentage points; the corresponding recalculated estimates are -0.171 for the placebo comparison and 0.021 and 0.125 for the active-treatment comparisons in the recalculation record. These discrepancies mean the two sets of numbers should not be presented as though they were a single analysis. In particular, the unadjusted recalculation for the Cohort II placebo comparison does not align with the sponsor-reported cohort-specific comparison.

The discrepancy flag is true, so the sponsor’s own analysis takes precedence. The sponsor-reported findings should be used to describe the trial’s reported primary tests, while recalculated values are useful as transparent, unadjusted checks based on summaries. The record does not explain the discrepancy’s cause in enough detail to identify a definitive explanation. It would be inappropriate to attribute it to a particular adjustment, data-handling rule, or subgroup definition without further documentation.

15. Multiplicity, Missing Data and Analysis Populations

The study includes multiple treatment comparisons: each boceprevir regimen is compared with placebo within each of two cohorts. It also lists several secondary outcomes and assessments at different treatment or follow-up times. When multiple hypotheses are tested, the chance of at least one result appearing statistically significant by chance can increase. Statistical plans may address this with a hierarchy, adjusted significance thresholds, or another prespecified approach. A multiplicity-control strategy is not reported in the registry record, so the reported p-values should not be assumed to have been adjusted unless the record says so. The sponsor’s named tests are reported, but the available information does not establish the full testing hierarchy.

The registry defines the primary analysis set as randomized participants who received at least one dose of study medication. It also gives a specific rule for missing primary endpoint data: a participant missing the follow-up week-24 result after an undetectable result at follow-up week 12 was to be considered to have SVR. That rule affects how this particular missing-data pattern is classified. The registry does not report a complete account of other missing values, exclusions, sensitivity analyses, or how missing outcomes in other patterns were handled. Those details matter because conclusions can depend on assumptions about participants without an observed endpoint.

The trial is described as randomized and double-masked, but detailed methods for sequence generation, allocation concealment, and maintenance of masking are not reported in the registry record. The exact covariates or strata used in the Cochran-Mantel-Haenszel analyses are also not stated. The primary population definition and the named analysis method are useful, but do not supply every detail needed for a full assessment of the statistical plan.

Finally, the trial separated participants into two cohorts and reported cohort-specific results. The registry does not report a formal test of whether treatment effects differ between cohorts. Separate estimates should not be interpreted as evidence of an interaction or as a direct statistical comparison between cohorts.

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 (1.1%), chest pain (1.1%), syncope (1.1%), suicidal ideation (1.1%), thrombocytopenia (0.8%).

The registry reports serious adverse event counts by treatment group, with the number at risk and the number affected. The PEG plus RBV group has 363 participants at risk and 31 with a serious adverse event. The 24-week boceprevir plus PEG and RBV group has 368 at risk and 42 affected. The 44-week boceprevir plus PEG and RBV group has 366 at risk and 45 affected. These counts are descriptive; they do not by themselves establish that one regimen caused more serious events than another. No comparative statistical analysis for these safety counts is reported in the registry record.

The most frequent serious adverse event terms listed include anaemia, chest pain, syncope, and suicidal ideation, each reported as 1.1%, and thrombocytopenia and pyrexia, each reported as 0.8%. These are the registry’s listed terms and percentages, not a complete account of all possible safety outcomes. Death counts are not reported in the registry record. The adverse-event groups are presented by regimen, without cohort-specific serious-event results in the available information.

Safety interpretation should account for group sizes, exposure and follow-up, definitions, and how events were collected. The registry does not provide enough detail to compare exposure-adjusted event rates or to determine the timing and duration of events. These figures describe what was posted, rather than establishing a causal safety difference.

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

The primary results describe SVR percentages at follow-up week 24 in this randomized trial population. The sponsor-reported comparisons show higher SVR percentages for both boceprevir regimens than for placebo with PEG and RBV in each cohort. The reported confidence intervals and p-values quantify statistical uncertainty under the sponsor’s analysis method; they do not answer every question about the size, relevance, or durability of the observed differences.

The endpoint is specifically the registry-defined undetectable HCV-RNA result at follow-up week 24, with the stated rule for missing week-24 data after an undetectable result at follow-up week 12. It is not a complete measure of all health outcomes or treatment experiences. These results do not by themselves describe adverse-event burden, quality of life, long-term outcomes beyond the stated assessments, or the balance between benefits and harms. Safety counts are posted separately and are descriptive.

The trial compared regimens that differed in whether they included boceprevir and in their planned treatment durations. The response-guided regimen’s detailed treatment rules are incomplete in the registry record. The reported primary comparisons are against placebo, not direct comparisons between the two active regimens. It would therefore be too strong to claim from these comparisons that one boceprevir duration is better than the other.

Results also apply to the trial’s enrolled population and the analysis set described in the registry. The record does not establish how findings generalize to populations or treatment settings not represented in the study. Statistical significance is not the same as clinical importance, and an observed group difference is not a guarantee of an individual outcome. No treatment recommendation follows from these statistics alone.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through both its design and its analysis. The primary outcome is a binary endpoint, so group percentages and absolute risk differences offer an interpretable summary of observed response. Confidence intervals add information about precision that a point estimate or p-value alone cannot convey. Reading the effect estimate, interval, and analysis method together gives a more complete statistical account.

The two cohorts also make the importance of population-specific precision visible. The sponsor reports positive comparisons in both cohorts, but the Cohort II intervals are wider than those in Cohort I. That pattern cautions against treating estimates from the cohorts as equally precise or assuming that a result in one cohort determines the magnitude in the other. The registry does not report a formal test of differences between cohort effects.

The record also provides an example of why sponsor-reported analyses and unadjusted recalculations need to be distinguished. The sponsor used a Cochran-Mantel-Haenszel chi-square approach, whereas the simple recalculations use posted summaries. The discrepancy flag makes clear that these estimates should not be blended. Transparent labeling of methods and precedence is necessary for readers to understand what each number represents.

Finally, the record shows the limits of registry-level reporting. It gives the endpoint definition and some analysis details, yet does not report the complete multiplicity plan, all missing-data procedures, or the original sample-size assumptions. A careful interpretation separates documented results from unanswered methodological questions rather than filling gaps with assumptions.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary endpoint relies on undetectable HCV-RNA at follow-up week 24 and a stated rule for a particular missing-data pattern. The registry does not describe all other missing-data handling or report sensitivity analyses. The impact of alternative assumptions about missing observations therefore cannot be assessed from the record.

Several comparisons and outcomes are listed, but a multiplicity strategy is not reported. This limits interpretation of the overall strength of evidence across all tests, especially for secondary outcomes. The detailed response-guided treatment rules are also incomplete, making it difficult to reconstruct exactly how treatment duration was determined for participants offered that strategy.

The cohort-specific comparisons have different levels of precision, and the registry does not report a formal treatment-by-cohort interaction test. Separate cohort estimates should not be treated as proof that effects differ or are the same between cohorts. The sponsor’s analysis and simple recalculations also show a flagged discrepancy; the cause is not resolved in the registry record. The sponsor-reported analysis takes precedence, but the discrepancy limits the extent to which the unadjusted recalculations can serve as a check.

For safety, the posted counts are descriptive, and there is no reported comparison adjusting for exposure or follow-up. The registry does not report death counts in the safety data described. The record also does not include the trial’s original sample-size rationale, complete randomization and masking procedures, or full statistical analysis plan. These omissions restrict independent assessment of design choices and analytical robustness.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Boceprevir in Previously Untreated Subjects With Chronic Hepatitis C Genotype 1 (Study P05216AM2) (COMPLETED) — NCT00705432.
• Registry record last updated 2017-04-07; status last verified 2017-03.
• Results first posted 2011-06-14.
• 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

NCT00705432 is a completed, randomized, double-masked, parallel phase 3 study of boceprevir or placebo with PegIntron and ribavirin in previously untreated adults with chronic hepatitis C genotype 1. The registry describes separate cohorts for White participants and Black participants, with placebo, response-guided boceprevir, and 44-week boceprevir regimens in each cohort.

The primary outcome was SVR at follow-up week 24, defined by undetectable plasma HCV-RNA under the registry’s stated missing-data rule. Sponsor-reported analyses found higher SVR percentages for each boceprevir regimen than for placebo within both cohorts. Their confidence intervals indicate less precision in Cohort II than in Cohort I. Because the record flags a discrepancy between sponsor analyses and simple recalculations, the sponsor’s own analyses take precedence.

Some secondary SVR results and serious adverse event counts are posted. The record does not report a complete multiplicity plan, all missing-data procedures, the original sample-size assumptions, or detailed results for every listed secondary outcome.