A Phase III Study of TMC435 in Treatment-naive, Genotype 1, Hepatitis C-infected Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase III Study of TMC435 in Treatment-naive, Genotype 1, Hepatitis C-infected Patients (NCT01292239), a randomized phase 3 study. The primary outcome is The Percentage of Participants With a Sustained Virologic Response at the End of Treatment (EOT) and 12 Weeks After the Last Dose of Treatment (SVR12).

2. Clinical Question

The central comparison is between two treatment regimens, not between TMC435 and no treatment: both groups received peginterferon alfa-2a and ribavirin. The trial record describes random assignment, double masking, and a parallel-group design. Its primary endpoint is a binary response: each participant either met the specified SVR12 definition or did not. The registry reports results for 123 participants in the TMC435 group and 60 in the placebo group in the primary analysis.

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group Phase III trial in Japan. The registry lists 183 participants enrolled and a completed study. The recorded start was 2011-02 and the primary completion was 2012-10. The sponsor was Janssen Pharmaceutical K.K.

Participants were treatment-naive and had chronic genotype 1 hepatitis C infection. The intervention group received TMC435 100 mg once daily with peginterferon alfa-2a and ribavirin for 12 weeks, then continued the latter two medicines. The regimen description says treatment was stopped at Week 24 for participants meeting specified early HCV RNA response criteria; the description ends after the word “All” and does not give the rest of that arm description. The placebo group received placebo with peginterferon alfa-2a and ribavirin for 12 weeks, then peginterferon alfa-2a and ribavirin until Week 48.

The planned treatment schedules were not identical in duration. The primary outcome was assessed at the end of treatment, which could be Week 24 or 48, and 12 weeks after the last dose, which could be Week 36 or 60. This outcome timing reflects the treatment schedule and follow-up definition recorded for the trial.

The primary analysis population was the Full Analysis Set. It included participants who received at least one dose of study drug, except those who did not meet major eligibility criteria and those without efficacy data available after study medication. The registry reports 123 participants in the TMC435 group and 60 in the placebo group for the primary outcome. The trial’s original allocation targets, sample-size justification, randomization details, and any protocol deviations 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: Treatment-naïve HCV-infected participants were assigned to 1 of 2 groups to receive TMC435 100 mg once daily with PegIFN alpha-2a and ribavirin (PR) until Week 12, followed by PR until Week 24 or 48 OR placebo with PR until Week 12, followed by PR until Week 48.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consisted of all participants who received at least one dose of study drug during the study except for those who did not meet the major eligibility criteria for the study and participants who did not have efficacy data available after treatment with study medication.

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 The Percentage of Participants With a Sustained Virologic Response at the End of Treatment (EOT) and 12 Weeks After the Last Dose of Treatment (SVR12), measured over EOT (up to Week 24 or 48) and 12 weeks after the EOT (up to Week 36 or 60).

The primary endpoint was the percentage of participants with a sustained virologic response at the end of treatment and 12 weeks after the last treatment dose, known as SVR12. A participant met this definition by having undetectable plasma HCV RNA at both specified assessments. The registry describes the end-of-treatment assessment as up to Week 24 or 48 and the later assessment as up to Week 36 or 60.

This is a binary endpoint at the participant level: the outcome is classified as response or no response under the stated definition. Expressing the result as a percentage makes the proportion meeting that definition comparable between the two randomized groups. The endpoint also requires that response be present after treatment has ended, rather than only during dosing. That is why its timing includes a follow-up assessment after the last dose.

The registry’s definition is specific to the reported RNA measurements and assessment times. It does not, by itself, describe every aspect of a participant’s later clinical course. The endpoint is used to assess virologic response in this trial; it should be interpreted as that measured outcome, not as a complete measure of health or as proof of an individual participant’s future outcome.

7. Results Posted in the Registry

• PBO 12 Wks + PR 48: 61.7% (37/60) versus 88.6% (109/123) on control; risk difference -27.0 percentage points (95% CI -40.5 to -13.4), risk ratio 0.70 (0.56–0.86); 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.

The Percentage of Participants With a Sustained Virologic Response at the End of Treatment (EOT) and 24 Weeks After the Last Dose of Treatment (SVR24)

• 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:
  • PBO 12 Wks + PR 48: 56.7% (34/60) versus 88.6% (109/123) on control; risk difference -32.0 percentage points (95% CI -45.7 to -18.2), risk ratio 0.64 (0.51–0.80); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for PBO 12 Wks + PR 48 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The Number of Participants With Viral Breakthrough

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • PBO 12 Wks + PR 48: 3.3% (2/60) versus 0.8% (1/123) on control; risk difference 2.5 percentage points (95% CI -2.3 to 7.3), risk ratio 4.10 (0.38–44.32); unadjusted two-proportion z-test p = 0.208.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PBO 12 Wks + PR 48 and the control. The interval gives the range of effects that remain compatible with the data.

The Number of Participants Demonstrating Viral Relapse

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • PBO 12 Wks + PR 48: 30.6% (15/49) versus 7.6% (9/118) on control; risk difference 23.0 percentage points (95% CI 9.2 to 36.7), risk ratio 4.01 (1.88–8.55); 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 PBO 12 Wks + PR 48 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover sustained response at a later follow-up time, changes in HCV RNA during treatment, undetectable RNA, viral breakthrough, viral relapse, ALT normalization, response-guided treatment completion, and plasma TMC435 concentrations. The registry lists nine posted secondary outcomes, but numerical results are included for only some of the outcomes represented in the available results. Results for outcomes without posted numerical values are not reported in the registry record.

Across the numerical secondary outcomes, the longer follow-up sustained-response result has the same broad direction as the primary response comparison. The event outcomes do not all follow a uniform pattern: the breakthrough counts are small, while the relapse comparison differs in direction from the primary response comparison. These endpoints have distinct definitions, follow-up periods, and analysis denominators, so the pattern should not be reduced to a single summary claim.

The secondary results complement the primary endpoint by addressing response durability and particular events. They do not independently confirm the primary finding in the same way as a prespecified replication would. Their interpretation is also affected by multiplicity: examining several outcomes creates more opportunities for apparently notable results even when each test is considered separately. The registry does not report an adjustment for multiple comparisons, and the secondary p-values shown for recalculated comparisons are unadjusted.

For that reason, secondary outcomes are best treated as supportive or exploratory context unless a prespecified testing hierarchy is documented. No such hierarchy is reported in the registry record. Results for each endpoint should be interpreted with its own denominator and uncertainty, rather than ranked solely by whether a p-value crosses a conventional threshold.

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

• The Percentage of Participants With a Sustained Virologic Response at the End of Treatment (EOT) and 24 Weeks After the Last Dose of Treatment (SVR24)
• The Percentage of Participants Who Achieved a Greater Than or Equal to 2 log10 IU/mL Drop From Baseline in Plasma Hepatitis C Virus Ribonucleic Acid (HCV RNA) at Each Time Point During Treatment and Follow-up
• The Percentage of Participants With Undetectable Plasma Levels of Hepatitis C Virus Ribonucleic Acid (HCV RNA) During Treatment and at the End of Treatment (EOT)
• The Number of Participants With Viral Breakthrough
• The Number of Participants Demonstrating Viral Relapse
• The Number of Participants With Abnormal Alanine Aminotransferase (ALT) Levels at Baseline Who Achieved Normal ALT Levels at the End of Treatment (EOT)
• The Percentage of Participants in the TMC435 Treatment Group Who Met Response Guided Treatment (RGT) Criteria and Completed Treatment With Peginterferon Alpha-2a (PegIFN Alpha-2a) and Ribavirin (RBV) at Week 24
• Plasma Concentrations of TMC435

9. Statistical Interpretation

10. Statistical Methods Explained

The main outcome is binary because each participant is classified according to whether the SVR12 definition was met. For a binary outcome, the percentage is the proportion of analyzed participants with the event of interest. The registry gives the group percentages and confidence intervals, and the recalculation compares those proportions without adjustment. A percentage is easy to interpret, but it does not show the distribution of outcomes beyond the response classification.

What does a confidence interval express?

In general, a confidence interval describes the uncertainty around an estimate under the assumptions of the statistical method. It is not a range containing every participant’s result, and it does not mean there is a specified probability that the fixed true value lies inside the particular interval. Wider intervals indicate less precision than narrower intervals when the same scale and method are being compared. The registry reports group intervals for the primary outcome and a separate interval for the sponsor’s comparison.

What is the role of the unadjusted comparison?

The recalculated comparison uses the posted outcome summaries to make a simple, unadjusted comparison between the trial groups. Such a calculation is useful as a transparent check on the direction and broad magnitude of the observed contrast. It does not reproduce every feature of a sponsor analysis if that analysis uses additional structure or adjustments. The recalculated p-value is reported as <0.001. It is not a substitute for the trial’s prespecified analysis, whose full specification is not reported in the registry record.

What does the sponsor analysis report?

The registry identifies the sponsor method as Cochran-Mantel-Haenszel and reports an estimate of 27.5, a 95% confidence interval from 14.38 to 40.56, and p < 0.001. In general, the Cochran-Mantel-Haenszel approach combines information across strata. The registry does not identify the stratification variables or explain the parameter notation, so those details should not be inferred. The posted results do not flag a discrepancy between the sponsor analysis and the recalculation.

How should p-values be read?

In general, a p-value measures how incompatible the observed data are with a specified null model, under the model’s assumptions. A small p-value is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary comparison has small reported p-values under both the recalculation and sponsor analysis. Interpretation should also consider the outcome definition, estimates, confidence intervals, and design rather than relying on a threshold alone.

Why do denominators matter?

The primary analysis uses the Full Analysis Set definition recorded by the registry. Secondary outcomes may use different numbers of participants, as illustrated by the listed denominators for viral relapse. A result is interpretable only in relation to its own analysis population and outcome definition. The registry does not report a full account of missing observations or the method used to handle them, so it is not possible to determine whether missingness affected each endpoint in the same way.

Why can event data be less stable?

In general, estimates based on few events may be imprecise and sensitive to small changes in counts. Ratios can become especially unstable when an event is uncommon. The viral breakthrough outcome has small observed counts in both groups, and its recalculated comparison has a confidence interval that includes no difference. This is a reminder to interpret sparse event results cautiously, rather than treating a point estimate as a precise description.

For event rates and binary endpoints, over-dispersion can matter when observations vary more than a model assumes. In general, ignoring over-dispersion can make uncertainty estimates too narrow. The registry does not report an over-dispersion assessment, and the main endpoint is presented as a participant percentage rather than a rate model. No claim about a model’s adequacy beyond the reported analysis can be made from the record.

11. Confidence Intervals and Precision

The primary group estimates are 88.6% for TMC435 and 61.7% for placebo. Their reported confidence intervals are 83.63 to 94.39 and 49.6 to 73.47, respectively. The intervals describe uncertainty around each group’s response percentage. The placebo interval is wider, so its estimate is less precise in the displayed results; the group also has fewer analyzed participants.

The sponsor’s comparison is reported as 27.5, with a 95% confidence interval from 14.38 to 40.56. The registry does not describe the parameter attached to that estimate beyond its method and notation, so the interval should be read on the scale intended by the sponsor analysis, not silently translated to another measure. The recalculated comparison is an unadjusted estimate, with its own reported interval in the statistical results.

In general, a confidence interval reflects sampling uncertainty under the method’s assumptions. It is not a guarantee that the true value is within the interval, nor does it capture all sources of uncertainty, such as limitations in the study population or missing-data handling. The interval width depends in part on the amount of information available and the observed data. A narrow interval can still be affected by systematic limitations, while a wide interval signals that a range of values remains compatible with the data.

The primary results are more informative than a p-value alone because the estimates and intervals show the observed response proportions and their precision. They do not establish the exact effect in a broader population, and they do not remove the need to consider the design, analysis population, or the way secondary outcomes were handled.

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 figures are planning illustrations based on the observed effect, not the trial’s original design justification. For these binary outcomes, the figures represent participants per arm. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The illustrations consider detecting the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a planning scenario designed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and model assumptions were correct. The 90% power column gives the corresponding planning count for a 90% chance. These are design calculations, not statements about the chance that the observed trial result is true. This is not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. That follows because a smaller contrast is harder to distinguish from random variation with the same precision. The figures are illustrations anchored to the observed effect, so they should not be treated as independent evidence for the effect’s size or as recommended sample sizes for a future study. The planning assumptions, outcome definition, analysis method, and target population would need to be considered together in any separate design exercise.

The outcomes in these planning illustrations are participant-level binary results. They are not total event counts from a time-to-event analysis. The registry does not report an original target enrollment calculation or its assumptions, so the planning numbers should remain separate from the study’s actual enrollment and analyzed group sizes.

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 = 0.886; treatment proportion p₁ = 0.617; average p̄ = 0.751.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6112 = 1.1979.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5807 = 0.4888.
4. n = (1.1979 + 0.4888)² / (-0.2695)² = 39.2, rounded up to 40 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 <- 0.886178861788618                          # control proportion
p1 <- 0.616666666666667                          # 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(1292239)
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 = 40 (80% power), 52 (90% power)
 75% of observed effect: n per arm = 64 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 128 (80% power), 170 (90% power)
power.prop.test: 39.2 
Simulated power at n = 40 per arm: 0.820 (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’s reported analysis uses the Cochran-Mantel-Haenszel method and gives an estimate of 27.5, a 95% confidence interval from 14.38 to 40.56, and p < 0.001. The recalculated unadjusted comparison uses the posted group results and reports p <0.001. Both analyses point in the same direction as the observed group percentages: SVR12 was more frequent in the TMC435 group than in the placebo group.

The record does not flag a discrepancy between the sponsor result and the recalculation. The sponsor analysis is the trial’s reported inferential result; the recalculation is a simple check based on the posted summaries and should not be presented as a replacement for it. The registry does not provide enough detail to establish the strata or exact parameter interpretation used in the sponsor analysis. Its reported estimate and interval should therefore be retained as recorded, without assuming additional methodological details.

The two p-values are not identical, which is unsurprising when analyses use different methods. Neither p-value measures clinical importance or removes uncertainty. Reading the estimates, intervals, endpoint definition, and analysis population alongside them gives a fuller account than treating statistical significance as the entire result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and multiple secondary outcomes. Testing or inspecting several outcomes can increase the chance of finding at least one apparently unusual result by chance. In general, multiplicity procedures—such as a prespecified testing sequence or an adjustment to significance thresholds—can help control that issue. The registry record does not report whether a multiplicity strategy was planned or applied, so the secondary findings should not be treated as though family-wise error control is established.

The reported sponsor analysis for the primary endpoint is identified as Cochran-Mantel-Haenszel. The registry does not report the analysis plan in enough detail to identify stratification variables, the full model specification, or whether interim analyses were planned or conducted. Those details are not reported in the registry record. The original sample-size justification is also not reported.

The primary analysis population is defined as the Full Analysis Set: participants who received at least one dose of study drug, excluding those who failed major eligibility criteria and those without efficacy data available after study medication. This definition is relevant because exclusions and missing outcomes can affect how closely an analysis reflects the randomized comparison. The record does not give a participant flow account or describe how missing values were handled for each endpoint. It is therefore not possible to determine whether missingness was assumed to be absent, handled by a particular imputation method, or addressed in another way.

These omissions do not change the reported percentages, but they limit assessment of how robust the results are to analysis choices. The registry’s definition of the analysis set, endpoint timing, and available denominators should be read alongside the results. More detailed protocol and analysis-plan information is not reported in the registry record.

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: vertigo positional (1.7%), malaise (1.7%), hepatic mass (1.7%), inclusion body myositis (1.7%), intervertebral disc protrusion (1.7%).

The registry reports serious adverse events in 4 of 123 participants in the TMC435 group and 6 of 60 participants in the placebo group. It also lists serious-event terms, each reported at 1.7%: positional vertigo, malaise, hepatic mass, inclusion body myositis, intervertebral disc protrusion, and dizziness. The record does not provide a basis for attributing each listed term to a particular group, so those terms should not be assigned to an arm.

The registry lists other adverse events for 123 of 123 participants in the TMC435 group and 60 of 60 in the placebo group. Death counts are not reported in the registry record. These figures describe reported events in the recorded groups; they do not establish that a treatment caused or prevented an event. Comparisons should account for the different group sizes, duration of treatment, event definitions, and the limited detail available in the registry summary.

Serious adverse event counts are not a complete account of all safety information. The record’s summary does not provide event timing, exposure-adjusted rates, severity grading for all events, or a full narrative of causality assessments. It should therefore be read as a limited description of the posted safety results.

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

The primary results show that the observed percentage meeting the registry’s SVR12 definition was higher in the TMC435 group than in the placebo group. Both groups received peginterferon alfa-2a and ribavirin, so the comparison concerns adding TMC435 rather than comparing treatment with no active background regimen. The confidence intervals and reported analyses convey uncertainty around the observed result, and the findings are specific to the trial’s enrolled and analyzed participants.

The result does not establish that every participant receiving one regimen would have the same outcome, nor does it determine an individual’s response. It does not by itself answer questions about outcomes beyond the measured endpoint and follow-up, or establish effects in populations not represented by this Japan-based, treatment-naive, genotype 1 trial. It also cannot isolate effects of the background medicines because both arms received them.

Statistical evidence and clinical meaning are related but distinct. A small p-value indicates incompatibility with a specified null model under its assumptions; it does not quantify benefit, guarantee replication, or establish whether a difference matters to patients. The endpoint is a virologic measure defined by undetectable plasma HCV RNA at specified times, not a complete measure of health.

Safety counts should likewise be interpreted as recorded events rather than causal conclusions. The registry summary has limited information about event attribution and missing data. Taken together, the posted results describe a comparative trial outcome and selected safety information; they do not replace a broader assessment of the full clinical evidence or establish results for treatments and populations not studied.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can be translated into an interpretable binary outcome: the proportion of participants meeting a defined response criterion in each group. Reporting both group percentages and uncertainty intervals allows readers to see the observed results and their precision, rather than relying only on a significance test. The sponsor’s reported method and the simple unadjusted recalculation also show why analysis method and estimand details matter when interpreting a comparison.

The trial’s combination-regimen design is important statistically. The contrast is between TMC435 plus peginterferon alfa-2a and ribavirin and placebo plus the same background medicines. The estimate therefore addresses the incremental comparison within that regimen, not the isolated effect of every medicine or a comparison with no treatment.

The secondary results demonstrate why endpoint definitions and multiplicity matter. Sustained response at a later time, breakthrough, and relapse describe different aspects of the trial course and can have different denominators. A consistent interpretation depends on treating these as related but distinct outcomes, and on recognizing that no multiplicity strategy is reported in the registry record.

Finally, the record shows the distinction between observed trial results and planning calculations. Illustrative sample sizes based on the observed effects can help explain how target effect size and power assumptions influence planning, but they are not the trial’s original design rationale. Keeping that distinction clear prevents a retrospective calculation from being mistaken for a prospective design decision.

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 results apply most directly to the trial’s recorded population: treatment-naive participants in Japan with chronic genotype 1 hepatitis C. The registry does not establish how well the estimates apply to people with different prior treatment histories, genotypes, settings, or eligibility characteristics. The background regimen and treatment schedules are also part of the comparison, limiting interpretation beyond these regimens.

The primary analysis excluded participants who did not meet major eligibility criteria and those without efficacy data after study medication, as well as including only participants who received at least one dose. The registry does not provide a full account of missing outcome data or how missingness was handled. This limits evaluation of potential effects of exclusions and incomplete follow-up.

The registry describes the TMC435 response-guided stopping condition but the arm description is incomplete in the record. It does not report the full statistical analysis plan, original sample-size justification, multiplicity approach, interim-analysis details, or stratification variables for the sponsor’s Cochran-Mantel-Haenszel analysis. Those omissions constrain assessment of prespecification and analytic choices.

Some secondary endpoints have limited event counts or use denominators different from the primary analysis. Their estimates may therefore be less precise or less directly comparable across outcomes. The registry also does not report numerical results for every listed secondary outcome. Safety information is summarized, but the displayed record does not include all details needed to assess timing, attribution, or exposure-adjusted comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase III Study of TMC435 in Treatment-naive, Genotype 1, Hepatitis C-infected Patients — NCT01292239.
• Registry record last updated 2014-01-17; status last verified 2013-12.
• Results first posted 2013-12-09.
• 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

NCT01292239 is a completed, randomized, double-blind, placebo-controlled Phase III parallel-group study sponsored by Janssen Pharmaceutical K.K. It enrolled 183 treatment-naive participants with chronic genotype 1 hepatitis C in Japan. The primary comparison was TMC435 with peginterferon alfa-2a and ribavirin versus placebo with the same background medicines.

For the Full Analysis Set, SVR12 was reported for 88.6% of 123 participants in the TMC435 group and 61.7% of 60 participants in the placebo group. The sponsor reported a Cochran-Mantel-Haenszel estimate of 27.5, with a 95% confidence interval from 14.38 to 40.56 and p < 0.001. The registry also lists secondary response, virologic-event, and safety outcomes, with incomplete statistical-plan and missing-data details.