Safety and Efficacy Study to Compare Continuous Infusion of Interferon With Standard of Care for Chronic Hepatitis C: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study to Compare Continuous Infusion of Interferon With Standard of Care for Chronic Hepatitis C (NCT00919633), a randomized phase 2 study. The primary outcome is Viral Load: Incidence of Sustained Virologic Response (SVR).

2. Clinical Question

The study was designed to evaluate safety and efficacy of continuous subcutaneous interferon alfa-2b delivery using an external pump, in combination with oral ribavirin, compared with standard treatment. The registry lists chronic hepatitis C as the condition and identifies the primary outcome as the number of participants with sustained virologic response. That endpoint concerns response after treatment has ended, rather than response during the treatment period.

The primary comparison is between each of the three interferon pump dose groups and the peginterferon group. The posted results report 4 participants with the endpoint among 28 in the comparator group, 7 among 25 in dose 1, 2 among 27 in dose 2, and 4 among 26 in dose 3. These are observed counts in small groups. They do not by themselves account for uncertainty, which is why the estimated differences and their confidence intervals are also important.

3. Trial Design

The registry identifies this as a Phase 2, randomized, single-masked, parallel-group study. Participants were assigned to one of four groups: three continuous-infusion interferon alfa-2b dose groups and one weekly peginterferon alfa-2b group. The registry record does not report the randomization procedure, the allocation ratio, or which people were masked.

Each pump group is described as receiving continuous subcutaneous interferon alfa-2b for 48 weeks. The comparator is described as peginterferon alfa-2b at 1.5 μg/kg by subcutaneous injection weekly for 48 weeks. The study summary also describes oral ribavirin in combination with treatment, and ribavirin is listed as an intervention. Group-level ribavirin details are not reported in the registry record. The dose amounts for the three pump groups are also not reported in the registry record.

The study began in 2009-06, had primary completion in 2012-07, and is marked completed. The total enrollment is listed as 116. The primary outcome is the number of participants with sustained virologic response, assessed 24 weeks after treatment was complete. The registry also reports rapid virologic response at Study Week 4 and early virologic response at Study week 12.

Although the registry lists a planned study design, it does not report the original sample-size justification, the intended statistical analysis plan, any interim analyses, or a detailed account of analysis populations. The registry record reports no formal analyses for the posted outcomes. Consequently, the comparisons discussed in the results should be read as descriptions of the posted counts and estimates, not as a reconstruction of the trial’s prespecified analysis plan.

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: 210 screened, 116 randomized, 106 received at least 1 dose of study drug.

Overall Study

Reasons for not completing this period:

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 Viral Load: Incidence of Sustained Virologic Response (SVR), measured over 24 weeks after treatment is complete.

The primary endpoint is the number of participants with a sustained virologic response, assessed 24 weeks after treatment is complete. It is a binary outcome at the participant level: each participant either meets the endpoint definition or does not. The registry reports counts rather than a continuous measure of viral load, despite the outcome title beginning with “Viral Load.” The specific laboratory threshold or operational definition used to classify a response is not reported in the registry record.

A response assessed after treatment has ended addresses whether the measured virologic outcome is sustained beyond the treatment period. This makes it different in timing and interpretation from rapid or early virologic responses, which the registry reports during treatment at Study Week 4 and Study week 12. Those secondary outcomes can describe earlier response patterns, but they are not substitutes for the primary endpoint measured after treatment completion.

For the primary endpoint, the registry reports 4 participants with a response in the peginterferon group, 7 in pump dose 1, 2 in pump dose 2, and 4 in pump dose 3. The posted comparison estimates express differences in the observed proportions between each pump group and the comparator. Because the endpoint counts are limited and the confidence intervals are broad, the estimates should be interpreted alongside their uncertainty rather than as precise treatment effects.

The endpoint is useful for comparing groups on a clearly defined participant-level outcome, but the registry’s limited outcome description matters. The response definition, handling of missing measurements, and analysis population are not reported in the registry record. Those omissions restrict how fully the endpoint can be interpreted or reproduced.

7. Results Posted in the Registry

• Group 1: Interferon Alfa-2b (Dose 1): 28.0% (7/25) versus 14.3% (4/28) on control; risk difference 13.7 percentage points (95% CI -8.1 to 35.6), risk ratio 1.96 (0.65–5.91); unadjusted two-proportion z-test p = 0.219.
• Group 2: Interferon Alfa-2b (Dose 2): 7.4% (2/27) versus 14.3% (4/28) on control; risk difference -6.9 percentage points (95% CI -23.2 to 9.4), risk ratio 0.52 (0.10–2.60); unadjusted two-proportion z-test p = 0.413.
• Group 3: Interferon Alfa-2b (Dose 3): 15.4% (4/26) versus 14.3% (4/28) on control; risk difference 1.1 percentage points (95% CI -17.9 to 20.1), risk ratio 1.08 (0.30–3.87); unadjusted two-proportion z-test p = 0.910.

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.

Rapid Virologic Response (RVR)

• 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:
  • Group 1: Interferon Alfa-2b (Dose 1): 16.0% (4/25) versus 7.1% (2/28) on control; risk difference 8.9 percentage points (95% CI -8.4 to 26.1), risk ratio 2.24 (0.45–11.20); unadjusted two-proportion z-test p = 0.310.
  • Group 2: Interferon Alfa-2b (Dose 2): 25.9% (7/27) versus 7.1% (2/28) on control; risk difference 18.8 percentage points (95% CI -0.3 to 37.9), risk ratio 3.63 (0.83–15.94); unadjusted two-proportion z-test p = 0.060.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 1: Interferon Alfa-2b (Dose 1) 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 Group 2: Interferon Alfa-2b (Dose 2) and the control. The interval gives the range of effects that remain compatible with the data.

Early Virologic Response (EVR)

• 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:
  • Group 1: Interferon Alfa-2b (Dose 1): 60.0% (15/25) versus 25.0% (7/28) on control; risk difference 35.0 percentage points (95% CI 10.0 to 60.0), risk ratio 2.40 (1.17–4.92); unadjusted two-proportion z-test p = 0.010.
  • Group 2: Interferon Alfa-2b (Dose 2): 48.1% (13/27) versus 25.0% (7/28) on control; risk difference 23.1 percentage points (95% CI -1.6 to 47.9), risk ratio 1.93 (0.91–4.08); unadjusted two-proportion z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group 1: Interferon Alfa-2b (Dose 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 2: Interferon Alfa-2b (Dose 2) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints describe earlier virologic responses during treatment: rapid virologic response at Study Week 4 and early virologic response at Study week 12. Taken together, the posted counts show that the pattern is not uniform across dose groups or timepoints. The apparent direction and size of differences vary, rather than forming a consistent pattern that independently confirms the primary outcome.

These outcomes are related to the primary sustained response because they measure virologic response at earlier stages, but they are not the same endpoint. An early response does not establish that a response was sustained 24 weeks after treatment was complete. The primary result remains the relevant posted endpoint for the study’s stated primary question, while the secondary results offer additional, less definitive context about response during treatment.

Secondary comparisons carry less weight because the registry lists multiple outcomes and several treatment groups, while no multiplicity adjustment or prespecified hierarchy is reported. When many comparisons are considered, some estimates may look notable by chance. In addition, the registry does not list formal reported analyses for these secondary outcomes. Their posted estimates are therefore best viewed as exploratory descriptions, not as independent confirmation of a treatment difference.

Interpretation is also constrained by what is absent: the registry record does not explain how missing measurements were handled, identify the analysis populations, or provide a detailed statistical plan. Without those details, it is difficult to determine whether the secondary results were analyzed consistently with the primary outcome or whether any comparisons were selected after examining the data. They can inform the overall pattern, but they should not outweigh the imprecise primary comparisons.

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

• Rapid Virologic Response (RVR)
• Early Virologic Response (EVR)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either had a sustained virologic response or did not. For a binary outcome, one basic summary is the proportion of participants with the event in each group. The registry posts the event counts and group sizes, along with comparison estimates for each pump group against the peginterferon group. These are group-level summaries; they do not adjust for participant characteristics or other possible differences between groups.

What does a risk difference describe?

A risk difference is the event proportion in one group minus the event proportion in the comparison group. A positive value means the event proportion was higher in the pump group for the direction used in these comparisons; a negative value means it was lower. A value of zero represents no difference on this scale. The primary estimates are 0.137 for dose 1, -0.069 for dose 2, and 0.011 for dose 3. They are estimates from the observed groups, not exact measurements of an underlying treatment effect.

The registry also posts risk ratios and odds ratios for the primary comparisons. A risk ratio compares the event proportions as a ratio, while an odds ratio compares event odds. These measures use different scales from the risk difference and can look numerically different even when they describe the same underlying group data. They are not interchangeable. In particular, an odds ratio should not be read as a direct difference in event probabilities. The registry does not report an adjusted model for these comparisons.

How should confidence intervals be read?

A confidence interval describes a range of values compatible with the observed estimate under a statistical procedure and its assumptions. Its width conveys precision: a narrower interval indicates less statistical uncertainty, while a wider interval indicates more. For a risk difference, an interval extending below and above zero includes both directions of difference as well as no difference. Every primary confidence interval extends across zero, so the estimates do not precisely resolve the direction of the group difference. Confidence intervals do not guarantee that the true value lies within a particular interval, and they do not capture every possible source of bias or uncertainty.

The posted p-values are unadjusted. A p-value is calculated under a null hypothesis and a set of statistical assumptions; it indicates how unusual data at least this incompatible with that null would be under those assumptions. It is not a measure of effect size, and a larger p-value does not demonstrate that two treatments are the same. Because three pump-dose comparisons are made against one comparator, multiplicity is relevant: considering several comparisons can increase the chance of at least one apparently notable result by chance. The registry record does not report a multiplicity adjustment or a prespecified approach to handling multiple comparisons.

What can the counts establish?

Counts make the event totals transparent, but they do not account for uncertainty by themselves. The group sizes are modest, and a small change in the number of observed events can move a proportion noticeably. The estimates and intervals are therefore more informative than treating the raw counts as definitive. At the same time, the interval calculations depend on statistical methods and assumptions. The registry record does not report the methods used to derive its own formal analyses, and no reported analyses are listed.

The primary outcome is a count of participants with an event, not a time-to-event outcome. The planning assumptions for the sample-size illustrations state that they use a normal approximation, a two-sided significance level of 0.05, and equal allocation between the two arms. They are illustrations based on fractions of the observed effect, rather than a record of the original trial design. These planning conventions do not establish what methods were used to plan or analyze the completed study.

For the secondary outcomes, the registry posts event counts at Study Week 4 and Study week 12 and provides unadjusted comparison estimates for some, but not all, group contrasts. The RVR estimates are posted for dose 1 and dose 2; a comparison estimate for dose 3 is not reported in the registry record. The EVR estimates are posted for all three dose groups. No reported analyses are listed for either secondary outcome. These results should be treated as exploratory descriptions, especially because multiple outcomes and group comparisons are present and no multiplicity strategy is reported.

Statistical precision is not the same as clinical importance. A narrow interval can still contain values that are not clinically important, and a wide interval can include both important benefit and harm. The registry does not report a threshold for clinical importance, so the clinical meaning of any particular difference cannot be determined from the posted estimates alone.

11. Confidence Intervals and Precision

The primary estimates are imprecise. For dose 1, the risk difference is 0.137, with a 95% confidence interval from -0.081 to 0.356. For dose 2, the estimate is -0.069, with a 95% confidence interval from -0.232 to 0.094. For dose 3, the estimate is 0.011, with a 95% confidence interval from -0.179 to 0.201. Each interval includes zero and also spans values in both directions. The estimates therefore leave considerable uncertainty about the size and direction of the group differences.

These intervals are wide relative to their point estimates, reflecting limited precision in the posted comparisons. The groups contain 25 to 28 participants each, and the primary endpoint occurred in only a small number of participants in each group. With relatively few observed events, the estimated difference can be sensitive to the observed counts. This makes it particularly important not to interpret a point estimate as if it were known without error.

A confidence interval is not a range of guaranteed values for an individual participant, nor does it incorporate every source of uncertainty. It describes sampling uncertainty under the method used to construct it. The registry record does not report the confidence-interval method or its assumptions. The registry also does not report how missing outcome data were handled, whether all randomized participants contributed to the analysis, or whether the posted estimates correspond to a prespecified analysis population.

The intervals do not establish equivalence or rule out potentially important differences. Nor do they show that differences exist simply because the interval includes values away from zero. The posted results are compatible with a range of underlying effects. Greater precision would require more information and, generally, more outcome data; the planning illustrations address sample sizes under stated assumptions but are not evidence that the original study had those properties.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations concern two-arm comparisons, with the required number expressed as participants per arm. The outcomes in these illustrations are counts of participants with an event, not time-to-event outcomes; therefore, the figures are participant counts per arm rather than total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect is a stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm that, under those assumptions and for the effect being considered, would give an 80% chance of detecting a difference using the stated test criterion. The 90% power column applies the same idea with a higher chance of detection, so it generally calls for more participants. These are planning illustrations, not a measure of how likely the completed trial was to detect its effects.

Each planning scenario uses a different fraction of the observed effect. Planning for 75% of the observed effect requires more participants than planning for 100% of the observed effect, and planning for 50% requires more still. Smaller effects are harder to distinguish from random variation, so detecting them with the same target power generally requires larger groups. The figures also vary substantially across comparisons because the observed effect sizes differ, and planning calculations based on unstable estimates from small groups can themselves be uncertain.

This is not observed power. It does not describe the probability that a particular result from the completed trial is true or that a treatment has an effect. It is a forward-looking illustration conditional on the selected assumptions and effect size; it cannot replace a confidence interval or an analysis of the observed data.

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 = 0.143; treatment proportion p₁ = 0.280; average p̄ = 0.211.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5775 = 1.1318.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5693 = 0.4791.
4. n = (1.1318 + 0.4791)² / (0.1371)² = 138.0, rounded up to 138 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 <- 0.142857142857143                          # control proportion
p1 <- 0.28                          # 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(919633)
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 = 138 (80% power), 185 (90% power)
 75% of observed effect: n per arm = 232 (80% power), 309 (90% power)
 50% of observed effect: n per arm = 486 (80% power), 650 (90% power)
power.prop.test: 138 
Simulated power at n = 138 per arm: 0.806 (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 study includes three pump-dose groups compared with one comparator, as well as a primary endpoint and two secondary endpoints. This creates multiple opportunities to examine differences. If each comparison is evaluated separately without adjustment, the chance of at least one apparently unusual result can increase. The registry record does not report whether the study used a formal multiplicity strategy, such as an adjustment to the significance criterion or a prespecified testing sequence. The posted comparison p-values are unadjusted, so they should not be interpreted as if they account for all the comparisons.

The registry identifies the primary endpoint, which helps distinguish it from secondary outcomes, but it does not provide a detailed analysis plan. It is not reported whether the three pump-dose comparisons were all prespecified, whether any one dose was the main comparison, or how the secondary endpoints were intended to be interpreted. Without those details, the relative confirmatory status of individual comparisons is unclear.

Missing-data handling is also not reported in the registry record. The record does not describe whether every randomized participant had an endpoint assessment, how missing viral-load measurements were classified, or whether any imputation or other missing-data method was used. The group counts and denominators are posted, but they do not by themselves explain participant flow from randomization through outcome assessment.

The analysis populations are not described. In particular, the registry record does not state whether the primary results use all randomized participants, participants who received treatment, or participants with evaluable endpoint data. These choices can affect the interpretation of a randomized comparison. No reported formal analyses are listed for the primary or secondary outcomes, and the sponsor’s intended statistical methods are not reported in the registry record. The posted estimates should therefore be read as unadjusted descriptions with uncertainty, rather than as a complete account of the trial’s planned confirmatory analysis.

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: pneumonia (8.0%), syncope (8.0%), anaemia (4.0%), type 2 diabetes mellitus (4.0%), bronchitis (3.8%).

The registry reports serious adverse events for all four groups. In the peginterferon group, 2 of 28 participants were reported as having a serious adverse event. The counts were 6 of 25 in pump dose 1, 5 of 27 in pump dose 2, and 6 of 26 in pump dose 3. These are group-level counts; the registry record does not provide a statistical comparison of serious adverse events between groups.

The record also lists several serious adverse-event terms with percentages: Pneumonia and Syncope at 8.0% each; Anaemia and Type 2 Diabetes Mellitus at 4.0% each; and Bronchitis and Cellulitis at 3.8% each. The listed terms are not accompanied by group-specific counts in the available record, so the percentages should not be assigned to a particular treatment group. The registry reports that other adverse events affected all participants at risk in each group, but does not give a detailed breakdown of those events in the registry record for this analysis.

Deaths are not reported in the registry record. Serious-event counts in groups of these sizes are descriptive and do not, by themselves, establish a comparative safety difference. The record does not provide event timing, duration, severity details beyond seriousness, or an adjusted safety analysis.

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

The posted results describe a randomized study comparing three continuous-infusion interferon alfa-2b regimens with weekly peginterferon alfa-2b. On the primary endpoint, the observed counts differed across groups, but the unadjusted risk-difference confidence intervals for all three pump-dose comparisons include zero and extend in both directions. The estimates do not precisely establish how the groups differ on sustained virologic response.

These results do not establish that the treatments are equivalent. Equivalence requires a prespecified margin and an analysis designed to evaluate whether the difference lies within that margin; neither is reported in the registry record. The results also do not establish that any pump dose is superior or inferior. The intervals are compatible with multiple possible underlying differences, and the p-values are unadjusted and do not resolve the uncertainty.

The secondary endpoints add information about response at earlier treatment timepoints, but they are not substitutes for sustained response after treatment. Their interpretation is limited by the multiple outcomes and comparisons, the lack of reported multiplicity handling, and the absence of formal analyses in the registry record. They should not be used alone to make a definitive claim about the primary endpoint.

The findings are specific to the groups, regimens, outcome definitions, and follow-up reported in this study. Important contextual details, including the exact dose amounts for the pump groups, the operational definition of sustained virologic response, missing-data handling, and analysis populations, are not reported in the registry record. The safety counts are descriptive and are not a formal comparative safety analysis.

In statistical terms, the central message is uncertainty, not proof of no difference. The posted estimates give a range of plausible group differences, but the record does not provide enough methodological detail to fully assess how the results were planned or analyzed. The results should be understood as registry-posted outcome data rather than as a complete account of the evidence needed to draw broader clinical conclusions.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it compares several active regimens with a single comparator while reporting relatively small group sizes and a binary primary endpoint. It illustrates why looking only at event counts or point estimates can be misleading: the direction of the observed difference varies across pump doses, and uncertainty around each estimate is substantial. Confidence intervals make that uncertainty visible.

It also highlights the distinction between a failure to demonstrate a difference and evidence that there is no difference. Each primary interval includes zero, but each also spans values away from zero. The data therefore do not precisely settle the direction or size of the comparisons. That interpretation is more informative than treating an unadjusted p-value as a yes-or-no verdict.

The multiple treatment comparisons and secondary outcomes raise questions about multiplicity. Without a reported strategy for managing multiple tests, nominal p-values warrant caution, particularly for exploratory outcomes. The absence of a reported formal analysis plan, missing-data methods, and analysis populations further limits assessment of how the posted estimates relate to the trial’s intended analysis.

Finally, the sample-size illustrations show how planning conclusions depend on assumed effect size and target power. They are distinct from the original trial’s design justification, which is not reported in the registry record, and they are not observed power. Keeping planning calculations, observed estimates, and inferential uncertainty separate is essential when interpreting a small clinical trial.

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.

Several limitations specific to this study constrain interpretation. The primary endpoint is reported as a number of participants with sustained virologic response, but the response threshold or laboratory definition is not described in the registry record. The group-level dose amounts for continuous interferon alfa-2b are also not reported, making it difficult to connect the dose-group results to specific administered doses. Although ribavirin is listed and the study summary describes its use, group-level details are not reported in the registry record.

The study has four groups with between 25 and 28 participants reported for the primary outcome. The resulting event counts are small, and the posted confidence intervals are broad. The registry lists 116 participants enrolled but does not explain participant flow or the relationship between enrollment and the outcome denominators. It also does not report whether the analysis included all randomized participants or only those with available outcome data.

Further limitations include the lack of a reported statistical analysis plan, original sample-size justification, multiplicity strategy, missing-data procedure, and interim-analysis information. No formal reported analyses are listed for the primary or secondary outcomes. The single-masked designation is not accompanied by an explanation of who was masked. These gaps prevent a full assessment of prespecification and analysis conduct.

The secondary outcomes are measured during treatment and are not equivalent to the primary endpoint measured after treatment. Their results involve multiple comparisons and should be interpreted cautiously. The safety data are also limited: serious-event counts are posted, but the listed serious-event terms lack group-specific counts, and deaths are not reported in the registry record. These limitations mean that the available data support a cautious statistical description, not a definitive comparative conclusion.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy Study to Compare Continuous Infusion of Interferon With Standard of Care for Chronic Hepatitis C — NCT00919633.
• Registry record last updated 2019-10-09; status last verified 2019-09.
• Results first posted 2014-04-30.
• 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, single-masked, parallel-group Phase 2 study of 116 participants with chronic hepatitis C. Three groups received continuous subcutaneous interferon alfa-2b by external pump for 48 weeks, and one group received weekly subcutaneous peginterferon alfa-2b at 1.5 μg/kg for 48 weeks.

The primary endpoint was the number of participants with sustained virologic response 24 weeks after treatment completion. Posted counts ranged from 2 to 7 across the four groups. Each unadjusted risk-difference confidence interval for a pump dose versus the comparator included zero. The registry also reports rapid and early virologic response outcomes and serious adverse-event counts.

The record does not report the original sample-size justification, a detailed analysis plan, multiplicity handling, missing-data methods, or analysis populations. The posted comparisons are therefore best read as estimates with substantial uncertainty and incomplete methodological context.