Sofosbuvir Plus Ribavirin Administered for Either 12 or 24 Weeks in Treatment-Naive and Treatment-Experienced Egyptian Adults With Chronic Genotype 4 Hepatitis C Virus (HCV) Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Sofosbuvir Plus Ribavirin Administered for Either 12 or 24 Weeks in Treatment-Naive and Treatment-Experienced Egyptian Adults With Chronic Genotype 4 Hepatitis C Virus (HCV) Infection (NCT01838590), a randomized phase 3 study. The primary outcome is Percentage of Participants With Sustained Virologic Response (SVR) at 12 Weeks After Discontinuation of Therapy (SVR12).

2. Clinical Question

The central statistical question is how the observed response proportions vary across treatment duration and prior treatment status, and how precisely those proportions and comparisons are estimated. The four reported groups are small, so the estimates should be read alongside their uncertainty rather than as exact predictions for other patients or settings. The registry record does not report a formal interaction analysis assessing whether the association between duration and response differs by treatment history. Accordingly, comparisons across the four group percentages are descriptive unless a posted analysis explicitly tests them.

3. Trial Design

This was a Phase 3, randomized, open-label study with a parallel-group design. Participants were assigned to receive sofosbuvir plus ribavirin for either 12 weeks or 24 weeks. No masking was used. The registry record lists 103 participants enrolled. The stated population was Egyptian adults with genotype 4 hepatitis C virus infection, including people who were treatment-naive and people who had previously been treated.

The outcome results are divided into four groups: 12 weeks among treatment-naive participants, 12 weeks among treatment-experienced participants, 24 weeks among treatment-naive participants, and 24 weeks among treatment-experienced participants. The reported group sizes for the primary endpoint are 25, 27, 24, and 27, respectively. These group-specific results matter because treatment history is part of the study question; combining the groups would obscure the separate patterns recorded for the two histories.

Random allocation is intended to reduce systematic differences between assigned groups, while open-label treatment means participants and study personnel were not masked to the assigned duration. The registry record does not report details of the allocation procedure, concealment, or any additional safeguards. It also does not report the original sample-size justification or the planned statistical analysis methods. The study is listed as completed, with a start date of 2013-03 and primary completion in 2014-05. These design features define the setting for interpreting the results but do not, on their own, establish how well the findings generalize beyond the enrolled population.

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: 141 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: participants with genotype 4 HCV infection who were randomized and received at least one dose of study drug

5. Baseline Characteristics

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

Population: Safety Analysis Set: participants who were randomized and received at least 1 dose of study drug

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Sustained Virologic Response (SVR) at 12 Weeks After Discontinuation of Therapy (SVR12), measured over Posttreatment Week 12.

The primary endpoint was the percentage of participants with sustained virologic response 12 weeks after discontinuing study treatment, called SVR12 in the registry record. It was defined as HCV RNA below the lower limit of quantitation, 25 IU/mL, at posttreatment week 12. The primary analysis population comprised participants with genotype 4 HCV infection who were randomized and received at least one dose of study drug.

SVR12 is a binary outcome for each participant: the participant either meets the stated RNA threshold at the specified follow-up time or does not. The group-level percentage describes the fraction meeting that definition. This endpoint is used to summarize virologic status at a fixed time after treatment has ended, rather than only while treatment is being taken. Its definition is tied to both a laboratory threshold and a particular follow-up time, so results from other time points are not interchangeable with SVR12.

The registry record also lists sustained virologic response at 4 and 24 weeks after treatment discontinuation as secondary outcomes, but their results are not reported in the registry record. The posted primary percentages therefore address the registered SVR12 definition only. They do not, by themselves, describe every later or earlier virologic outcome, explain why a participant did or did not meet the threshold, or establish that the same response pattern would occur in populations not represented in this study.

7. Results Posted in the Registry

• SOF+RBV 12 Weeks, TE: 70.4% (19/27) versus 84.0% (21/25) on control; risk difference -13.6 percentage points (95% CI -36.1 to 8.8), risk ratio 0.84 (0.62–1.13); unadjusted two-proportion z-test p = 0.244.
• SOF+RBV 24 Weeks, TN: 91.7% (22/24) versus 84.0% (21/25) on control; risk difference 7.7 percentage points (95% CI -10.5 to 25.8), risk ratio 1.09 (0.89–1.35); unadjusted two-proportion z-test p = 0.413.
• SOF+RBV 24 Weeks, TE: 88.9% (24/27) versus 84.0% (21/25) on control; risk difference 4.9 percentage points (95% CI -13.7 to 23.5), risk ratio 1.06 (0.85–1.31); unadjusted two-proportion z-test p = 0.606.

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 Experiencing Virologic Relapse

• 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:
  • SOF+RBV 12 Weeks, TE: 29.6% (8/27) versus 16.0% (4/25) on control; risk difference 13.6 percentage points (95% CI -8.8 to 36.1), risk ratio 1.85 (0.64–5.40); unadjusted two-proportion z-test p = 0.244.
  • SOF+RBV 24 Weeks, TN: 4.2% (1/24) versus 16.0% (4/25) on control; risk difference -11.8 percentage points (95% CI -28.3 to 4.6), risk ratio 0.26 (0.03–2.17); unadjusted two-proportion z-test p = 0.171.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SOF+RBV 12 Weeks, TE and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SOF+RBV 24 Weeks, TN and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary outcomes covering sustained virologic response at other follow-up times, on-treatment virologic failure, and virologic relapse. Results are posted for virologic relapse, with percentages varying across the treatment-duration and prior-treatment groups. The results for sustained virologic response at 4 and 24 weeks and for on-treatment virologic failure are not reported in the registry record. The available secondary information is therefore incomplete relative to the listed outcomes.

At a broad level, relapse is related to the primary endpoint because it describes a virologic event after treatment, whereas SVR12 records whether the specified RNA threshold is met at a fixed posttreatment time. The two outcomes are not interchangeable: one is a response status at a time point and the other is a reported event over a stated period. The registry record does not provide a joint participant-level analysis connecting relapse events to the primary endpoint, so the secondary results should not be used to reconstruct or explain individual SVR12 outcomes.

Secondary outcomes generally carry less evidential weight when they are numerous, not fully reported, or not accompanied by a stated testing plan. Repeated statistical testing increases the chance of finding an apparently notable result by chance if no multiplicity approach is used. The registry record does not report a multiplicity adjustment, testing hierarchy, or sponsor-reported analyses for these outcomes. The posted secondary data are therefore best treated as descriptive context rather than as confirmatory evidence that resolves the uncertainty in the primary comparisons.

The overall secondary pattern can help identify what was measured beyond SVR12, but missing outcome results and absent analysis details limit how much can be concluded. The secondary findings do not remove the uncertainty around the primary contrasts or establish a separate causal explanation for the differences between observed groups.

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

• Percentage of Participants With Sustained Virologic Response at 4 and 24 Weeks After Discontinuation of Therapy (SVR4 and SVR24)
• Percentage of Participants Experiencing On-treatment Virologic Failure
• Percentage of Participants Experiencing Virologic Relapse

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help clarify what the posted results can and cannot establish. The explanations below describe general statistical concepts and then relate them to the figures reported for this study. They do not imply that the registry record specifies a particular method where none is reported.

What does a percentage measure?

For a binary outcome such as SVR12, each participant is classified according to whether the endpoint definition was met. A group percentage summarizes the proportion of participants in that group who met it. The primary results are presented separately by treatment duration and prior treatment status. These percentages describe the observed participants; they are not guarantees about outcomes for other people. Small denominators make percentages sensitive to the outcome of individual participants, which is why the group sizes and uncertainty estimates matter when comparing them.

What is a risk difference?

A risk difference expresses the difference between two event proportions on the probability scale. A value of zero corresponds to equal proportions. A positive or negative estimate indicates which group had the higher observed proportion, given the order of the comparison. Here, the reported comparisons use the 12-week treatment-naive group as the reference. For SVR12, a negative risk difference means the comparison group’s observed response proportion was lower than the reference proportion; a positive estimate means it was higher. The estimates are recalculated, unadjusted comparisons based on posted summary data, not reported sponsor analyses.

The registry record also includes relative measures, such as risk ratios and odds ratios, in the comparison data. These express contrasts on different scales from the risk difference. A risk ratio compares proportions as a ratio, while an odds ratio compares odds. Each scale can convey a different aspect of the same data, and all are affected by the limited group sizes. The primary narrative emphasizes the risk-difference estimates and their confidence intervals because those directly describe the absolute contrast on the probability scale. The registry record does not list a sponsor-selected comparative measure or adjusted model.

How should a p-value be understood?

A p-value describes how unusual data at least as incompatible with a specified null model would be if that model were true, subject to the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The p-values listed for these comparisons are unadjusted. They should be read with the estimates and confidence intervals, not as stand-alone decisions. The registry record does not report a multiplicity adjustment or a prespecified testing hierarchy.

Because the p-values accompany recalculated comparisons, they should not be mistaken for results of a sponsor-reported analysis. The registry record lists no reported analysis results. The recalculations are simple unadjusted comparisons from the posted summary statistics, and the record does not report whether these specific contrasts were part of the original statistical plan.

Why does the confidence interval matter?

A confidence interval shows the range of effect estimates reasonably compatible with the data under the method’s assumptions. A narrow interval conveys greater precision than a broad interval. In this study, each risk-difference interval includes zero and also spans values on both sides of zero. That pattern reflects substantial uncertainty about the direction and size of each contrast. It does not prove that the groups are identical; nor does it establish a difference. The intervals should be interpreted as estimates of uncertainty, not as a range containing a fixed proportion of individual participants’ outcomes.

What does randomization contribute?

Random allocation can help balance participant characteristics across assigned groups on average, reducing some sources of confounding in a comparison. It does not ensure that groups are identical, especially when group sizes are limited. The registry record identifies the study as randomized but does not report the allocation sequence, concealment procedures, or baseline balance results. Without those details, the extent to which the randomization process was implemented as intended cannot be assessed from the registry record.

The open-label design means the assigned duration was not masked. The primary outcome is based on a laboratory RNA threshold, but the record does not report blinded outcome assessment or laboratory procedures. Open-label status is therefore a feature to consider, while its specific influence on this endpoint cannot be determined from the posted information.

Why can over-dispersion matter?

For some outcome types, observed variability can exceed what a simple statistical model assumes. This is called over-dispersion. When it is present and not accommodated, standard errors can be too small and confidence intervals too narrow. The primary outcome is a binary percentage, and the registry record does not report an over-dispersion assessment or a model-based adjustment. This general issue does not establish that over-dispersion occurred in this study; it illustrates why the exact analysis method and its assumptions matter.

In general, statistical interpretation also depends on how missing observations, protocol deviations, and analysis populations were handled. The primary population is identified as randomized participants who received at least one dose, but missing-data procedures and sensitivity analyses are not reported in the registry record. Those omissions limit assessment of robustness. The percentages and unadjusted comparisons remain useful descriptions of the posted results, but their interpretation should stay within the boundaries of the reported methods and data.

11. Confidence Intervals and Precision

Precision concerns how tightly the data estimate an outcome or contrast. A confidence interval communicates uncertainty around an estimate: narrower intervals indicate more precision, while wider intervals leave more possible values compatible with the data and method. The SVR12 percentages are based on group sizes ranging from 24 to 27 participants, so the estimates are based on relatively small groups. The registry record does not provide confidence intervals for the individual group percentages.

For the three recalculated risk differences against the 12-week treatment-naive reference, the confidence intervals were -0.361 to 0.088, -0.105 to 0.258, and -0.137 to 0.235. All include zero and extend in both directions from it. The estimates therefore leave uncertainty about whether each comparison group had a lower or higher response proportion than the reference. Their breadth also means that the data do not pinpoint the size of any contrast. These intervals are not evidence that the groups are equivalent.

Confidence intervals are often misunderstood as assigning a probability to the true effect after the data have been observed. In general statistical interpretation, the stated confidence level describes the long-run performance of the interval procedure under its assumptions. It does not mean that a fixed percentage of participants’ outcomes fall inside the interval. The registry record does not state the confidence level for these recalculated comparison intervals, so no confidence level should be inferred from the posted values alone.

Precision is distinct from whether a result is important. A precise estimate can be small or large, and an imprecise estimate can include a range of effects that would be interpreted differently in context. The posted data support descriptive reporting of the group outcomes, but the limited group sizes and broad comparison intervals constrain the strength of conclusions about differences.

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 figures are illustrations of how sample requirements change under stated assumptions; they are not the original trial’s design justification, which is not reported in the registry record. For these binary outcomes, figures are participants per arm, not total events. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as its starting point and considers detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect. The registry record does not report the trial’s own original sample-size assumptions.

The 80% power column describes an illustrative number of participants per arm that, under those assumptions and for the specified effect, would give the calculation an 80% chance of rejecting the null model if that effect were the true one. The 90% power column uses a higher target chance and therefore generally requires more participants per arm. For example, planning around the full observed contrast between the 12-week treatment-naive reference and the 12-week treatment-experienced group gives 148 participants per arm for 80% power and 198 participants per arm for 90% power. For planning for 75% of the observed effect, the corresponding figures are 250 and 333 participants per arm; for 50% of the observed effect, they are 528 and 706 participants per arm.

Smaller effects are harder to distinguish from random variation, so detecting a smaller effect generally requires more participants. These figures depend on using observed effects as planning inputs; observed effects from small groups can be unstable and should not be treated as reliable predictions of future effects. This is not observed power. The registry record does not report the original rationale for the enrolled sample size, nor does it report that these illustrative calculations informed the trial design.

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 = 0.840; treatment proportion p₁ = 0.704; average p̄ = 0.772.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5935 = 1.1632.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5856 = 0.4928.
4. n = (1.1632 + 0.4928)² / (-0.1363)² = 147.6, rounded up to 148 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 <- 0.84                          # control proportion
p1 <- 0.703703703703704                          # 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(1838590)
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 = 148 (80% power), 198 (90% power)
 75% of observed effect: n per arm = 250 (80% power), 333 (90% power)
 50% of observed effect: n per arm = 528 (80% power), 706 (90% power)
power.prop.test: 147.6 
Simulated power at n = 148 per arm: 0.802 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists five outcome measures and multiple comparisons across treatment duration and treatment history. Testing several outcomes or contrasts creates a multiplicity issue: when many hypotheses are examined, the chance of at least one apparently unusual result can increase. Statistical plans sometimes address this through a prespecified primary outcome, a testing hierarchy, or an adjustment to the threshold for interpretation. The registry record identifies SVR12 as the primary outcome, but does not report a multiplicity strategy for the other outcomes or comparisons.

The three risk-difference comparisons are simple unadjusted recalculations from the posted summary data. The registry record lists no sponsor-reported analysis results. The unadjusted p-values should therefore not be read as confirmation that these comparisons were planned in advance, nor as corrected evidence across the full set of outcomes. The original statistical analysis plan and details of any interim analyses are not reported in the registry record.

The primary analysis population is described as randomized participants who received at least one dose of study drug. That identifies who was included in the stated population, but it does not explain how missing endpoint measurements were handled, whether all randomized participants were included in any other analysis, or how treatment discontinuation and protocol deviations were addressed. Those procedures are not reported in the registry record. Sensitivity analyses assessing the influence of missing data are also not reported.

These omissions affect assessment of the analysis, not the meaning of the observed percentages themselves. Readers can describe the posted results and their uncertainty, while recognizing that the registry record does not establish how missing observations, multiple testing, or planned analyses were handled. The absence of those details limits evaluation of whether the reported comparisons represent a prespecified confirmatory analysis or an exploratory examination of the outcome data.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cerebral ischaemia (2.0%), dyspnoea (2.0%).

The serious adverse event figures are reported by treatment duration, not separately by treatment history. In the 12-week group, 0 of 52 participants were recorded as affected by serious adverse events. In the 24-week group, 2 of 51 were recorded as affected. The registry record lists cerebral ischaemia and dyspnoea as the top serious event terms, each reported as 2.0%. These are descriptive safety counts and terms; they do not establish that treatment duration caused an event or that the groups differ reliably in safety.

Other adverse events are listed for 34 of 52 participants in the 12-week group and 38 of 51 in the 24-week group. These counts should not be conflated with serious adverse events: the record reports them as a separate category. Death counts are not reported in the registry record.

Safety comparisons require caution because the groups are small and the registry record does not provide a statistical comparison, event-level exposure time, or a complete narrative of event severity and relatedness. A count of participants affected also does not necessarily equal the total number of events, since a participant may experience more than one event. The posted figures describe what the record reports, without establishing a causal relationship or a complete safety profile.

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

The results describe SVR12 among Egyptian adults with genotype 4 HCV infection who were randomized and received at least one dose of study drug. The registry reports separate response percentages for treatment-naive and treatment-experienced participants assigned to each of the two treatment durations. These observations show how the endpoint was distributed in this study’s groups; they do not by themselves determine which duration is preferable or establish that differences between groups are reproducible.

The unadjusted comparison intervals are broad and include zero. That means the data leave substantial uncertainty about the direction and size of the contrasts. It does not mean that there is no difference, and it does not demonstrate equivalence. The listed p-values likewise do not measure clinical importance or the probability that a particular conclusion is true. There is no sponsor-reported comparison analysis in the registry record to provide an alternative adjusted interpretation.

The outcomes also have a defined scope. SVR12 is based on HCV RNA below the stated threshold at posttreatment week 12. It does not summarize all possible clinical outcomes, all later virologic status, treatment experience, or safety. Results for several listed secondary outcomes are not reported in the registry record. The serious adverse event counts are descriptive and do not establish causation.

Generalizability is limited to the extent that the enrolled population and study setting differ from other populations or care settings. The registry record identifies Egyptian adults with genotype 4 infection, but does not provide enough detail to assess every source of variation in eligibility, care, or outcome measurement. The appropriate reading is therefore a bounded one: the posted data characterize the observed groups in this completed randomized study, with limited precision and important analysis details not reported. They should not be turned into medical advice or a claim about an individual’s likely outcome.

17. Why This Trial Matters Statistically

This study illustrates why a randomized comparison and an estimate’s precision answer different questions. Randomization is a design feature intended to support fair comparisons between assigned groups. Yet even in a randomized study, small group sizes can leave substantial uncertainty around estimated differences. The posted SVR12 percentages give a direct description of the observed outcomes, while the broad risk-difference intervals show that those observations do not tightly determine the comparative effect.

The division by treatment history is also statistically important. The outcome percentages are not identical across the treatment-naive and treatment-experienced groups, so presenting only an overall summary would hide relevant structure in the results. At the same time, separate subgroup descriptions do not demonstrate that treatment history changes the effect of duration. The registry record does not report a formal interaction analysis, and the group sizes limit precision for subgroup-specific contrasts.

The record also distinguishes outcomes that are listed from outcomes whose results are actually reported. Secondary outcomes can provide useful context, but incomplete results and no reported multiplicity plan make it difficult to assess them as confirmatory evidence. Similarly, recalculated unadjusted contrasts can help explain the posted summary data, but they are not a substitute for a fully documented sponsor analysis and its prespecified methods.

Finally, the illustrative planning calculations show how sample requirements depend on the effect size one aims to detect. Their purpose is to explain statistical planning, not to retroactively validate the trial’s size. The original design assumptions are not reported in the registry record. Taken together, these features make the study useful for understanding the relationship between design, outcome definition, subgroup structure, and uncertainty—while emphasizing that the numerical pattern is more informative when its limits are explicit.

18. Limitations

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

The primary outcome groups contain 24 to 27 participants each, which constrains precision. The comparison intervals are broad, and the registry record does not report confidence intervals for the individual group percentages. Separate results by treatment history are valuable descriptively, but small groups make it difficult to distinguish a stable subgroup pattern from random variation. No formal interaction analysis is reported.

The design was open-label, with no masking. The primary endpoint uses a laboratory RNA threshold, but details about outcome assessment and laboratory procedures are not reported in the registry record. The record also does not report the allocation procedure or concealment details, so those aspects of trial conduct cannot be evaluated from the posted information.

Important statistical details are absent: the original sample-size justification, the analysis plan, any interim analyses, handling of missing data, sensitivity analyses, and multiplicity procedures are not reported in the registry record. No sponsor-reported analysis results are listed. The comparisons discussed are unadjusted recalculations from the posted summary data and should not be mistaken for analyses specified in the original protocol.

Results are also incomplete across the outcomes listed in the record. SVR4, SVR24, and on-treatment virologic failure results are not reported in the registry record. Safety figures are descriptive, and death counts are not reported. Finally, the study population is specifically Egyptian adults with genotype 4 HCV infection; the registry record does not establish how well the results apply to populations outside that setting. These limitations affect precision, completeness, and the scope of interpretation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Sofosbuvir Plus Ribavirin Administered for Either 12 or 24 Weeks in Treatment-Naive and Treatment-Experienced Egyptian Adults With Chronic Genotype 4 Hepatitis C Virus (HCV) Infection — NCT01838590.
• Registry record last updated 2015-05-22; status last verified 2015-05.
• Results first posted 2015-05-22.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, randomized, open-label, parallel-group Phase 3 study sponsored by Gilead Sciences. It enrolled 103 Egyptian adults with genotype 4 hepatitis C virus infection and compared sofosbuvir plus ribavirin administered for 12 weeks or 24 weeks. The start date was 2013-03, and primary completion was 2014-05.

The primary outcome was SVR12, defined as HCV RNA below the lower limit of quantitation, 25 IU/mL, at posttreatment week 12. Results were reported separately by treatment duration and prior treatment status. The recalculated unadjusted comparisons against the 12-week treatment-naive group have broad confidence intervals that include zero. Several statistical-plan details and results for listed secondary outcomes are not reported in the registry record.