The Effect of Boceprevir in Russian Participants Diagnosed With Chronic Hepatitis C Genotype 1 (P08160): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effect of Boceprevir in Russian Participants Diagnosed With Chronic Hepatitis C Genotype 1 (P08160) (NCT01425203), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Sustained Virologic Response At Follow-up Week 24 (SVR24) Among Participants Who Received At Least One Dose of Any Trial Medication (Full Analysis Set Population).

2. Clinical Question

The question concerns the proportion meeting a defined virologic endpoint, not the amount of change in an individual participant's viral load. The registry record describes a randomized, double-masked, parallel-group phase 3 trial. The stated primary hypothesis was that the percentage achieving SVR would be higher with BOC + PR than with PBO + PR. The record also lists early virologic response at treatment week 8 and SVR24 in a modified intent-to-treat population as secondary outcomes. Those outcomes address related but distinct questions: one concerns an earlier treatment response, while the other uses a narrower analysis population for the later response endpoint.

3. Trial Design

The registry record identifies NCT01425203 as a phase 3, randomized, double-masked, parallel-group trial. It lists enrollment as 238 and the condition as chronic hepatitis C genotype 1. The official title describes a Russian study including previously untreated participants and participants whose prior treatment with pegylated interferon plus ribavirin had failed. The record names Merck Sharp & Dohme LLC as sponsor and marks the study completed.

The principal comparison was between response-guided boceprevir with peginterferon alfa-2b and ribavirin (RGT BOC + PR) and placebo with peginterferon alfa-2b and ribavirin (PBO + PR). Both arm descriptions include an initial period of PR before the additional study drug or matched placebo. The response-guided strategy then used BOC + PR followed by placebo + PR. The control-arm description states that participants received BOC-matched placebo after the initial PR period and describes subsequent treatment for up to 44 weeks; the record's wording for this arm is not fully consistent with that description, so it does not support a more detailed reconstruction of the control treatment sequence.

A crossover arm was available for participants assigned to the PBO + PR control arm who failed a futility rule at treatment week 12 or 24. Those participants received BOC + PR after crossover. For the primary SVR24 analysis, participants who switched from the placebo control arm to crossover were considered failures and are not reported in that endpoint's arm results. The crossover arm has no primary endpoint result listed, while adverse-event data are listed for that group.

The registry record gives arm-specific analysis populations for the outcomes, which need not match the enrollment figure. The primary endpoint included participants who received at least one dose of any trial medication. The mITT secondary SVR24 endpoint instead included those who received at least one dose of experimental trial drug. The registry record does not report a more complete account of recruitment, concealment, masking procedures, or the original design assumptions.

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: Of 238 randomized participants, 237 received at least 1 dose of peginterferon alpha-2b (PEG) + ribavirin (RBV) \[PR\] and comprised the Full Analysis Set (FAS). 4 discontinued (DC) treatment during the PR lead-in phase and did not receive BOC or Placebo (PBO). 27 from PBO Arm failed the futility time point and were rolled over into Crossover Phase.

Treatment Phase

Reasons for not completing this period:

Crossover Phase

Reasons for not completing this period:

Follow-up Phase

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS); all randomized participants who received at least 1 dose of any trial medication (PEG, RBV, or BOC) in the Treatment Phase. Participants in the PBO Control Arm who switched to the Crossover Arm were considered failures for SVR24 in this analysis and are not reported here.

5. Baseline Characteristics

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

Population: Baseline Characteristics were reported only for the Full Analysis Set (FAS), which consisted of all randomized participants who received at least 1 dose of any trial medication (PEG, RBV, or BOC) in the Treatment Phase. The Crossover Arm is not included as these participants originally started the study in the PBO + PR Control Arm at Baseline.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Sustained Virologic Response At Follow-up Week 24 (SVR24) Among Participants Who Received At Least One Dose of Any Trial Medication (Full Analysis Set Population), measured over Follow-up Week 24 (up to 72 weeks).

The primary endpoint is the percentage of participants achieving sustained virologic response at follow-up week 24 (SVR24). The record defines response as an undetectable plasma HCV-RNA level at follow-up week 24. It also specifies that a participant missing follow-up week 24 data was considered a responder if HCV-RNA was undetectable at follow-up week 12. The stated timeframe is follow-up week 24, up to 72 weeks.

SVR24 is a binary outcome: each participant is classified as meeting or not meeting the stated response definition, and the arm result is the percentage classified as responders. This endpoint summarizes whether viral RNA was detectable at the specified follow-up assessment under the registry's rules. It does not describe the timing or trajectory of viral change during treatment, which is a different question addressed in part by the secondary early virologic response outcome.

A sustained follow-up endpoint is used to assess whether an undetectable result is present after treatment rather than only at an earlier treatment visit. The registry's missing-visit rule matters because it determines how a subset of participants is classified when the primary follow-up measurement is unavailable. The registry record does not report additional sensitivity analyses for alternative missing-data assumptions. The primary population was the full analysis set: randomized participants who received at least one dose of any trial medication. Participants in the PBO control arm who crossed over were classified as failures for this analysis and are not included in the reported primary arm results.

7. Results Posted in the Registry

• RGT BOC + PR: 74.8% (119/159) versus 46.2% (36/78) on control; risk difference 28.7 percentage points (95% CI 15.7 to 41.6), risk ratio 1.62 (1.26–2.09); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants Achieving SVR24 Among Participants Who Received At Least One Dose of Experimental Trial Drug (Modified Intent-To-Treat [mITT] Population)

• 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:
  • RGT BOC + PR: 76.3% (119/156) versus 46.8% (36/77) on control; risk difference 29.5 percentage points (95% CI 16.5 to 42.5), risk ratio 1.63 (1.27–2.10); 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 RGT BOC + PR than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving Early Virologic Response (EVR) At Treatment Week (TW) 8

• 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:
  • RGT BOC + PR: 87.4% (139/159) versus 42.3% (33/78) on control; risk difference 45.1 percentage points (95% CI 33.0 to 57.2), risk ratio 2.07 (1.58–2.70); 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 RGT BOC + PR than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question in two directions. SVR24 in the modified intent-to-treat population examines the same follow-up endpoint using a population defined by receipt of experimental trial drug. Early virologic response at treatment week 8 addresses an earlier response during treatment rather than sustained response at follow-up. The posted percentages for both outcomes follow the same broad direction as the primary result, with higher response proportions in the BOC + PR group than in the PBO + PR control group.

This consistency adds context: the direction is not limited to the primary full analysis set endpoint alone, and the early measure points in a similar direction before the later follow-up assessment. But the secondary findings are not exact replicas of the primary comparison. The mITT outcome changes the analysis population, and the early response endpoint measures a different timepoint and clinical state. Their estimates therefore answer related but distinct questions.

The registry reports unadjusted secondary significance results, and it does not report a multiplicity procedure. When several outcomes are examined, the chance of obtaining at least one apparently notable result can increase if each is assessed separately without accounting for the full set of tests. Accordingly, the secondary p-values carry less weight than a prespecified primary analysis with a clear analysis plan. They are best read as supportive evidence and descriptive context, not as independent proof of multiple separate effects.

The registry record lists two secondary outcomes and sponsor analyses for each. It does not report whether further outcomes were measured but not posted, how the secondary endpoints were prioritized, or whether the analysis plan specified a hierarchy. The secondary results can therefore reinforce the broad pattern while leaving uncertainty about the implications of testing multiple outcomes. They should not displace the primary endpoint as the central inferential result.

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

• Percentage of Participants Achieving SVR24 Among Participants Who Received At Least One Dose of Experimental Trial Drug (Modified Intent-To-Treat [mITT] Population)
• Percentage of Participants Achieving Early Virologic Response (EVR) At Treatment Week (TW) 8

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is SVR24?

The primary measure is a binary outcome summarized as a percentage. A participant either meets the registry's SVR24 definition or does not. The definition depends on HCV-RNA being undetectable at follow-up week 24, with the specified follow-up week 12 rule for a participant missing week 24 data. The percentage gives the share meeting that definition in each arm. It is not a mean viral load and does not indicate how far apart individual viral loads were.

What does the difference compare?

A difference in percentages compares the response proportions between the BOC + PR group and the PBO + PR control group. A positive difference in the direction used in the posted comparison means the response proportion is higher in the experimental group. The sponsor reports an adjusted difference in percentages using the Miettinen and Nurminen method. The simple recalculation is an unadjusted risk difference based on the posted summary statistics. Adjustment and the choice of method can lead to estimates that are close but not identical. The two results should therefore be identified by their method and scale rather than blended into one estimate.

How should the p-value be understood?

A p-value assesses how compatible the observed data are with a specified null model, assuming the analysis model and its assumptions. A small p-value is evidence against that null model; it is not the probability that the null hypothesis is true, and it does not quantify the size or practical importance of an effect. The sponsor's primary analysis reports p < 0.001, while the simple unadjusted recalculation reports p < 0.001. These values come from different procedures and should be read as reported rather than combined.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the data and the method's assumptions. Its width communicates precision: a narrower interval indicates less statistical uncertainty about the estimated contrast, while a wider interval indicates more. The sponsor reports a 95% confidence interval for its adjusted difference, and the recalculation reports a 95% confidence interval for the unadjusted risk difference. The interval does not guarantee that the true value lies within its limits, and it does not account for every possible source of bias or uncertainty.

Why distinguish the analysis populations?

The primary full analysis set includes randomized participants who received at least one dose of any trial medication. The secondary mITT SVR24 analysis includes participants who received at least one dose of experimental trial drug. Changing the analysis population can change which participants contribute to the endpoint and therefore can change the estimated response proportion. For the primary analysis, the record specifies that control-arm participants who crossed over were considered failures and are not reported in the primary result. The registry record does not report further details about handling other missing observations or any sensitivity analysis of the endpoint classification rule.

Why use planning illustrations?

The planning figures use a stated fraction of the observed effect to illustrate the number of participants per arm under specified assumptions. Such illustrations are not a reconstruction of the trial's original design calculation. Their purpose is to show how planning requirements depend on the effect targeted, the significance level, allocation, and approximation used. Smaller target effects generally require more participants to achieve the same planned power, all else held constant. The original protocol's sample-size justification and design assumptions are not reported in the registry record.

These methods answer different questions. The arm percentages describe observed response proportions, the risk difference describes an absolute contrast, the confidence interval conveys uncertainty around an estimate, and the p-value evaluates compatibility with a null model. None substitutes for a full assessment of trial conduct, missing data, endpoint relevance, or the applicability of the findings to other settings. The registry record identifies the sponsor's method for the primary comparison but does not report all details of the statistical analysis plan.

11. Confidence Intervals and Precision

The primary sponsor analysis reports an adjusted difference in percentages of 29.2 percentage points, with a 95% confidence interval from 16.4 to 41.5. This interval expresses uncertainty around the adjusted contrast under the Miettinen and Nurminen method. Its limits are on the same percentage-point scale as the adjusted estimate. The interval does not describe the range of individual participant responses or the probability that a particular participant will respond.

The unadjusted recalculation gives a risk difference of 0.287, with a 95% confidence interval from 0.157 to 0.416. That estimate and interval use the proportion scale and are based on the posted summary statistics. The sponsor and recalculated estimates are close in direction and magnitude, but the scales and methods differ. The registry record does not flag a discrepancy between them. The sponsor's adjusted result remains the analysis reported by the trial.

Both intervals have limits above zero, so the estimated contrasts are compatible with a higher SVR24 percentage in the BOC + PR group under the methods used. The interval limits are more informative than a p-value alone because they indicate a range of effect sizes consistent with the data, including uncertainty about the size of the difference. They do not resolve uncertainty from unreported features such as the detailed handling of missing data or the full analysis plan.

Precision is not the same as validity. An estimate can have a confidence interval that is relatively concentrated while still being affected by limitations in trial conduct, population selection, or endpoint classification. The primary analysis population and the crossover-failure rule are relevant to interpreting the contrast. The registry record does not provide confidence intervals for the separate arm percentages, so the reported precision information concerns the between-group 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 values are participants per arm, not total event counts. They are illustrations based on the observed effect and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set at the stated fraction of the observed effect. These assumptions describe the planning illustrations, not the original design rationale; the trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified target effect under those planning assumptions, if that effect is real and the assumptions hold. The 90% power column gives the corresponding per-arm planning number for a higher chance of detection. Greater planned power generally requires more participants, all else held constant. The rows that plan for 75% or 50% of the observed effect target smaller effects than the row using the full observed effect. Smaller effects are harder to distinguish from random variation, so the planning figures increase as the target effect becomes smaller.

These figures are not observed power. They do not describe the probability that the completed trial detected its result, and they do not replace the trial's actual results or confidence intervals. Because the calculations use the observed effect as their starting point, they are illustrative rather than an independent confirmation of the effect. Planning for a future study would require choices about the target effect and design assumptions that are not established by these calculations alone.

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 = 0.462; treatment proportion p₁ = 0.748; average p̄ = 0.605.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6913 = 1.3550.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6609 = 0.5562.
4. n = (1.3550 + 0.5562)² / (0.2869)² = 44.4, rounded up to 45 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 <- 0.461538461538462                          # control proportion
p1 <- 0.748427672955975                          # 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(1425203)
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 = 45 (80% power), 59 (90% power)
 75% of observed effect: n per arm = 82 (80% power), 110 (90% power)
 50% of observed effect: n per arm = 189 (80% power), 253 (90% power)
power.prop.test: 44.4 
Simulated power at n = 45 per arm: 0.811 (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 comparison uses the Miettinen and Nurminen method and is described as an adjusted difference in percentages. It reports a 29.2 percentage-point difference, a 95% confidence interval from 16.4 to 41.5, and p < 0.001. This is the trial's own posted analysis and should be distinguished from the simple unadjusted recalculation based on the arm summary statistics.

The recalculation gives a risk difference of 0.287, with a 95% confidence interval from 0.157 to 0.416 and p < 0.001. Its result is on the proportion scale and is not adjusted using the sponsor's stated method. The closeness in direction of the results is reassuring as a descriptive cross-check, but differences in scale and method mean they are not interchangeable. The registry record does not identify a discrepancy.

The sponsor's analysis also appears in the secondary endpoint results: the mITT SVR24 comparison and the early virologic response comparison are each reported using the same named method, with their own adjusted differences and confidence intervals. Those results relate to different populations or timepoints and should be interpreted as separate analyses. The registry record does not provide enough detail to determine all adjustment variables or reproduce the sponsor's method from the posted information. The sponsor's reported estimates and procedures therefore remain the appropriate account of its analysis, while the recalculation serves only as a simple unadjusted check.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary endpoint and two secondary outcomes. It reports comparison p-values for those analyses, but a multiplicity adjustment or testing hierarchy is not reported in the registry record. When several statistical tests are conducted, interpreting each p-value as though it were the only test can overstate the strength of evidence across the collection of outcomes. This concern is most relevant to the secondary analyses, which should be treated as supportive rather than as multiple independent confirmations.

The primary SVR24 definition includes an explicit rule for missing follow-up week 24 data: a participant with undetectable HCV-RNA at follow-up week 12 was considered a responder. The primary population is also specified as randomized participants who received at least one dose of any trial medication. Control-arm participants who switched to crossover were considered failures for this endpoint and are not reported in the primary arm results. These rules are important because an endpoint percentage depends on both the response definition and the population included.

Further details about missing observations are not reported in the registry record. In particular, the record does not explain how other missing HCV-RNA measurements were classified, whether additional imputation or sensitivity analyses were performed, or how robustness to alternative assumptions was assessed. The endpoint's stated follow-up week 12 exception should therefore not be taken as a complete account of all missing-data handling.

The secondary mITT SVR24 analysis uses a different population definition from the primary full analysis set. The registry record does not provide a detailed account of the reasons for the population difference or a full participant-flow description for each analysis. It also does not report whether subgroup analyses by prior treatment history were planned or how those analyses would be controlled for multiple testing. These omissions limit assessment of the complete analysis strategy; they do not alter the reported endpoint definitions and estimates.

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: neutropenia (6.9%), hypertension (2.6%), adverse event (1.3%), accidental overdose (1.3%), prostatitis (1.3%).

The adverse-event record gives serious adverse event counts and the numbers at risk by arm. Serious adverse events were reported for 17 of 159 participants in the RGT BOC + PR group, 9 of 78 in the PBO + PR control group, and 1 of 27 in the crossover arm. These are counts, not a comparison adjusted for follow-up time or other participant characteristics. The crossover group is a separate group in the safety listing and should not be merged into either randomized arm when interpreting the posted counts.

The record also lists other adverse events affecting 153 of 159 participants in the RGT BOC + PR group, 71 of 78 in the PBO + PR control group, and 22 of 27 in the crossover arm. Among the listed serious-event terms, neutropenia is reported at 6.9%, hypertension at 2.6%, and adverse event, accidental overdose, and prostatitis at 1.3% each; intestinal obstruction is listed at 0.6%. These terms are the registry's listed serious-event categories, not a complete description of every event experienced.

Deaths are not reported in the registry record. The listed counts alone do not establish that one treatment strategy is safer than another. The record does not provide the detail needed to account for event timing, duration of exposure, severity beyond serious-event classification, or causal attribution for each event.

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

The posted primary results show a higher observed SVR24 percentage in the RGT BOC + PR group than in the PBO + PR control group for the stated full analysis set. The sponsor-reported adjusted contrast has a 95% confidence interval whose limits are above zero, and the sponsor reports p < 0.001. The simple unadjusted recalculation is directionally consistent. These findings describe the registry's comparison and endpoint rules; they do not establish an outcome for every participant or guarantee a similar result in another population.

The result does not by itself establish how the effect varies across previously untreated participants and participants with prior treatment failure. Although both populations are described in the official title, subgroup estimates are not reported in the registry record. The record also does not report the details needed to judge every potential influence of missing measurements, adherence, or the crossover process on the outcome.

The endpoint is a defined virologic response at follow-up, not a direct measure of symptoms, liver outcomes, quality of life, or long-term disease course. Those outcomes are not reported in the primary result. Likewise, the response percentages do not establish the complete balance of benefits and harms. The adverse-event listings provide counts and selected serious-event terms, but not a full comparative assessment of exposure, timing, or attribution.

The secondary endpoints provide a broadly similar pattern but carry less inferential weight because the registry does not report multiplicity adjustment. The findings should therefore be understood as a statistical account of the specified trial comparison, not as a stand-alone recommendation or a substitute for clinical judgment. The registry record does not report evidence sufficient to generalize beyond the enrolled study population and treatment strategies.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation should distinguish observed arm percentages from the between-group estimate. The percentages describe outcomes within each group, while a risk difference directly contrasts the proportions. The sponsor's adjusted difference and the simple unadjusted recalculation are close in direction but arise from different methods and scales. Reporting both with their corresponding confidence intervals makes clear which result belongs to the trial's stated analysis and which is a summary-statistic check.

The analysis also demonstrates that the population definition is part of the estimand. The primary full analysis set, the secondary mITT population, and the crossover rule determine which participants contribute to each endpoint and how some outcomes are classified. Comparisons across endpoints cannot be understood solely by comparing percentages when the analysis populations or timepoints differ.

Confidence intervals help focus attention on both the direction and uncertainty of an estimated difference, rather than relying only on a thresholded p-value. The secondary outcomes also illustrate why multiplicity matters: related endpoints can add context, but multiple unadjusted tests should not automatically be treated as separate definitive findings. Finally, the planning illustrations show how required sample sizes depend on the target effect and the stated assumptions, while remaining distinct from the original trial design and from any claim about observed power.

Together, these issues make transparent reporting of endpoint definitions, analysis populations, methods, and missing-data rules essential. Some of those elements are reported clearly, while other analysis-plan details are not reported in the registry record. That distinction helps readers separate what the posted results support from questions the record leaves unresolved.

19. Limitations

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

The registry record does not report the original sample-size justification or the assumptions used to design the trial. The planning illustrations based on the observed effect cannot fill that gap. Detailed information about randomization procedures, allocation concealment, and how masking was maintained is also not reported in the registry record, despite the listed randomized and double-masked design.

The primary SVR24 analysis has a defined missing-week-24 rule, but other missing-data handling and sensitivity analyses are not reported in the registry record. The crossover-failure rule is specified for the primary outcome, yet the record does not provide a full account of how crossover affected follow-up, exposure, or other analyses. The control arm's treatment-sequence description is not fully consistent in its wording, limiting detailed reconstruction of that strategy from the registry entry alone.

Subgroup results by prior treatment status are not reported in the registry record, although the official title identifies previously untreated participants and participants with prior treatment failure. The record also does not report a multiplicity plan for the secondary outcomes, or a hierarchy for interpreting them. These omissions limit assessment of whether the secondary analyses were prespecified and how their p-values should be interpreted across the full set of tests.

The adverse-event listing gives counts, arm denominators, and selected serious-event terms, but deaths are not reported in the registry record. More detailed information about event timing, exposure-adjusted comparisons, severity, and attribution is also not reported. Consequently, the posted safety figures are descriptive and do not provide a complete comparative safety analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The Effect of Boceprevir in Russian Participants Diagnosed With Chronic Hepatitis C Genotype 1 (P08160) — NCT01425203.
• Registry record last updated 2021-02-08; status last verified 2021-01.
• Results first posted 2014-08-18.
• 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

NCT01425203 is a completed phase 3 randomized, double-masked, parallel-group trial of boceprevir with peginterferon alfa-2b and ribavirin compared with placebo with the same background medicines in Russian participants with chronic hepatitis C genotype 1. The official title includes previously untreated participants and participants whose prior pegylated interferon plus ribavirin treatment had failed.

The primary endpoint was SVR24 in the full analysis set, with a specified rule for some missing follow-up week 24 measurements and crossover participants classified as failures. The registry reports a higher SVR24 percentage in the RGT BOC + PR group than in the PBO + PR control group and a sponsor-reported adjusted difference of 29.2 percentage points. Secondary outcomes show a similar broad direction, while multiplicity and several analysis details are not reported in the registry record.