Hepatitis C Translating Initiatives for Depression Into Effective Solutions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Hepatitis C Translating Initiatives for Depression Into Effective Solutions (NCT01143896), a randomized na study. The primary outcome is Number of Patients Who Initiated Hepatitis C Antiviral Treatment Within 12 Months of Enrollment.

2. Clinical Question

The question links a depression-care intervention to a hepatitis C treatment process: whether antiviral treatment was initiated. The registry’s background explains that depression and substance use can be reasons patients with chronic hepatitis C are considered ineligible for antiviral treatment. That rationale describes the study’s motivation; it does not establish that every participant had those barriers or that changing depression care necessarily changed treatment eligibility.

The comparison is between assignment to the collaborative-care approach and usual care, rather than between specific antidepressant drugs or counseling treatments. The trial also recorded quality of hepatitis C care and medication adherence as secondary outcomes. Those measures provide context about care processes, but the primary question is specifically about antiviral treatment initiation within the stated follow-up period.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. Participants were allocated to depression collaborative care or usual care. The study is listed as completed, with enrollment of 309. Its phase is recorded as not applicable. The sponsor was the VA Office of Research and Development. The registry dates the study start to 2012-02 and primary completion to 2014-09.

The intervention arm received a depression collaborative-care model described as stepped care. A depression care manager monitored symptoms and self-management, and the listed steps included watchful waiting and treatment recommendations involving counseling or pharmacotherapy. The registry’s description of one later step is incomplete, so the full intervention protocol is not reported in the registry record. The usual-care arm received depression screening with the same PHQ-9 screener, without participation of the depression collaborative-care team.

The primary outcome was a binary measure of antiviral treatment initiation during 12 months after enrollment. The registry states that the primary population was intent to treat. The posted arm summaries report 11 participants with initiation among 114 in collaborative care and 7 among 128 in usual care. These are the outcome denominators posted for the comparison; the registry record does not explain how they relate to enrollment or describe the handling of participants without endpoint data.

The trial’s allocation sequence, concealment procedures, site count, detailed eligibility criteria, and specific rules for participant follow-up are not reported in the registry record. Nor are the trial’s original sample-size assumptions or a detailed statistical analysis plan. The posted comparisons are unadjusted calculations from arm-level summaries, and the registry reports no analyses in its analysis listing. Thus, the posted results can be described, but the record does not establish that the displayed comparisons reproduce a prespecified sponsor analysis.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: intent to treat

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: A total of 292 participants completed baseline interviews.

6. Primary Endpoint

The registry lists the primary outcome as Number of Patients Who Initiated Hepatitis C Antiviral Treatment Within 12 Months of Enrollment, measured over 12 months.

The primary endpoint counts participants who initiated hepatitis C antiviral treatment within 12 months of enrollment. A participant was classified as having initiated treatment if they received at least one prescription of interferon during that period; otherwise the endpoint was classified as not initiated. The registry identifies the outcome as dichotomous and states that the target population for the primary outcome was intent to treat.

This endpoint captures whether treatment was started, not whether a participant completed antiviral therapy, responded to it, or experienced a particular clinical outcome. It also does not measure depression symptoms directly. Its use reflects the study’s stated rationale: collaborative depression care was intended to address a potential barrier to antiviral treatment in hepatitis C care. Whether that pathway operated as intended cannot be determined from the initiation count alone.

In the posted results, initiation was recorded for 11 of 114 participants assigned to depression collaborative care and 7 of 128 assigned to usual care. The endpoint is useful for comparing the observed frequency of treatment initiation between the randomized groups, while the confidence interval helps convey how uncertain the size and direction of that difference remain. The registry does not report further detail on the prescription-record sources, adjudication procedures, or handling of incomplete follow-up.

7. Results Posted in the Registry

• Arm 1: Depression Collaborative Care: 9.6% (11/114) versus 5.5% (7/128) on control; risk difference 4.2 percentage points (95% CI -2.5 to 10.9), risk ratio 1.76 (0.71–4.40); unadjusted two-proportion z-test p = 0.216.

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.

Quality of Hepatitis C Care: Quality Indicators: Proportion of QIs Received

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Arm 1: Depression Collaborative Care: mean 0.89 versus 0.83 on control; difference 0.06 (95% CI 0.02 to 0.10), standardized effect d = 0.34; z-test p = 0.008.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Arm 1: Depression Collaborative Care than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Medication Adherence: Medication Possession Ratio

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Arm 1: Depression Collaborative Care: mean 0.83 versus 0.78 on control; difference 0.05 (95% CI -0.01 to 0.11), standardized effect d = 0.23; z-test p = 0.077.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 1: Depression Collaborative Care and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the posted mean estimates are both in the direction of higher values in the collaborative-care arm. The evidence is not equally precise across the two comparisons: the quality-of-care interval lies above the no-difference value, whereas the medication-adherence interval includes it. This pattern gives some context for the primary result, but it does not resolve the uncertainty around antiviral treatment initiation.

The endpoints are related to aspects of hepatitis C care, but they measure different processes from the primary outcome. Quality indicators summarize receipt of specified care processes, and medication possession ratio describes medication availability as defined for that measure. Neither is a direct substitute for the binary endpoint of receiving an interferon prescription within 12 months. A favorable pattern in secondary measures cannot establish that the intervention changed the primary outcome, and an uncertain primary estimate does not erase the separate information in those secondary measures.

The posted secondary comparisons are unadjusted. Their p-values do not account for the fact that the registry reports multiple outcomes, and multiplicity handling is not reported in the registry record. When several outcomes are examined, the chance of at least one apparently unusual result can increase; this is a general statistical concern. Without a reported testing hierarchy or adjustment plan, the secondary p-values should be treated as exploratory evidence rather than definitive confirmation.

Secondary outcomes can still be useful. They can describe whether observed differences appear consistent across related care processes and can help identify questions for future studies. Here, the overall direction is broadly favorable to collaborative care, but the endpoint-specific uncertainty and lack of reported multiplicity procedures counsel restraint. The primary result remains the direct evidence for the trial’s main question, and its confidence interval remains compatible with effects on both sides of no difference.

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

• Quality of Hepatitis C Care: Quality Indicators: Proportion of QIs Received
• Medication Adherence: Medication Possession Ratio

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute?

Random allocation is intended to make the groups comparable, on average, with respect to factors that could influence outcomes. In general, this makes a between-group comparison more interpretable than a comparison of groups formed by treatment choice alone. Randomization does not guarantee that every relevant characteristic is balanced in a particular trial, and it does not remove uncertainty from limited outcome data. The registry identifies the allocation as randomized, but details of sequence generation and concealment are not reported in the registry record.

Why is the primary outcome analyzed as a binary result?

The endpoint assigns each participant to one of two categories: antiviral treatment was initiated during the defined period, or it was not. The posted arm summaries therefore give event counts and the number of participants in each outcome denominator. A risk is the proportion of participants in a group who experienced the event. A risk difference compares those proportions by subtraction; it describes the absolute contrast in the event probability. The posted risk difference is 0.042. Positive values indicate a higher observed event proportion in the intervention group under the comparison’s stated direction.

A risk ratio compares the two risks by division, while an odds ratio compares the odds of the event. These relative measures use different scales and should not be interpreted as interchangeable with the risk difference. Here the posted estimates are a risk ratio of 1.764 and an odds ratio of 1.846. Their confidence intervals are wide, so the point estimates alone would give an incomplete picture. General: relative measures can appear large even when the absolute event frequency is low; it is therefore helpful to consider both relative and absolute summaries when interpreting a binary endpoint.

What does an unadjusted comparison mean?

The posted primary comparison is calculated from the group summaries without adjustment for other variables. An unadjusted comparison is transparent and can be derived from the group-level event counts, but it does not account for covariates or any additional modeling decisions. The registry does not report an adjusted primary analysis, covariates, or an analysis method for a sponsor-reported result. The displayed p-value and confidence interval should accordingly be understood as unadjusted recalculations, rather than as a documented adjusted or prespecified sponsor analysis.

The primary outcome is identified as intent to treat, a principle that generally analyzes participants according to their randomized assignment, regardless of treatment received after allocation. The registry does not provide enough detail to establish how missing outcome information was handled or whether the posted outcome denominators reflect every participant assigned to each arm. The intent-to-treat label is useful, but it does not by itself describe the practical procedures used to preserve that population in an analysis.

How should the mean-based secondary outcomes be read?

The quality-of-care measure is a proportion of quality indicators received, and medication adherence is described as a medication possession ratio. Both are reported as means with standard deviations in the two groups. A mean difference expresses the intervention-group mean minus the usual-care mean. The posted differences are 0.06 for quality of care and 0.05 for medication adherence. Their confidence intervals and unadjusted p-values give information about the compatibility of the observed contrasts with a range of possible underlying differences.

For a continuous measure, the standard deviation describes variation among observations within a group; it is not the same as the standard error of the group mean. In general, a standard error reflects the precision of an estimated mean and depends on both variation and the amount of information in the sample. The registry posts standard errors for the two secondary outcomes, but it does not report a detailed statistical plan for their analysis. These distinctions matter because a group can have substantial participant-level variability while its mean is estimated with greater or lesser precision depending on the amount of data.

The posted mean comparisons are also unadjusted recalculations. They should not be interpreted as adjusted effects, and their p-values do not indicate whether a formal hierarchy among outcomes was used. The registry’s analysis listing reports no analyses, and no multiplicity procedure or prespecified ordering of the secondary endpoints is reported in the registry record.

What does a confidence interval add?

A confidence interval represents uncertainty in an estimate under the assumptions of the statistical method. General: a wider interval indicates less precision, while an interval that includes the no-difference value leaves open the possibility that the underlying contrast could be absent under that method. For the binary primary outcome, the risk-difference interval spans -0.025 to 0.109. It includes zero, which is the value corresponding to no absolute difference. The interval should not be read as a guarantee that the true effect lies within its endpoints; it is a method-based summary of uncertainty, not a prediction about individual outcomes.

What can and cannot be inferred from the analysis record?

The registry provides outcome definitions, group summaries, recalculated comparisons, and planning illustrations. It does not report the trial’s original sample-size justification, its complete analysis plan, interim analyses, handling of missing data, or multiplicity procedures. General: these decisions can affect how estimates and tests are interpreted, particularly when several endpoints are assessed. Their absence from the registry record limits what can be concluded about prespecification and analysis choices, but it does not alter the arithmetic of the posted summary comparisons.

11. Confidence Intervals and Precision

Precision describes how tightly the data locate an estimated effect. For the primary risk difference, the posted estimate is 0.042, and its 95% confidence interval runs from -0.025 to 0.109. The range includes zero and extends to both negative and positive values. Thus, the point estimate favors a higher initiation proportion with collaborative care, but the interval does not pin down the direction or size with confidence. It is compatible with a small negative difference, no difference, or a positive difference that is larger than the point estimate.

The interval is important because the event counts are limited relative to the outcome denominators. In general, estimates based on fewer observed events tend to be less precise, although precision also depends on the statistical method and the observed data. The posted risk-ratio interval, 0.708 to 4.398, and odds-ratio interval, 0.691 to 4.935, are also broad. Both include the relative no-difference value of one. These intervals reinforce that the relative magnitude is uncertain, even though the point estimates are above one.

The secondary quality-of-care mean difference has a 95% confidence interval from 0.016 to 0.104, which lies above zero. The medication-adherence mean-difference interval, from -0.005 to 0.105, includes zero. These intervals differ in their relation to the no-difference value, but neither changes the fact that they are secondary comparisons without reported multiplicity adjustment. A confidence interval that excludes zero should not be taken as proof of a clinically important effect; the registry does not provide a threshold for clinical importance.

Confidence intervals describe uncertainty under the calculation’s assumptions and do not account automatically for every possible source of bias, incomplete follow-up, or analysis selection. The record does not report methods for addressing those issues. Precision is therefore only one part of interpretation: the outcome definition, trial conduct, analysis choices, and the limits of the registry record also matter.

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 expressed as participants per arm for the continuous and binary outcomes in this trial; they are not total event counts. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. These are planning illustrations based on the observed effects, not the trial’s original design assumptions; those original assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect is the true effect and the assumptions hold. The 90% power column gives the corresponding per-arm planning figure for a design with a 90% chance. In general, higher target power requires more participants, all else equal. The figures are not observed power for this completed trial and should not be read as a retrospective measure of how likely the trial was to find its observed result.

Each planning row scales the target from the full observed effect to a smaller fraction of it. The rows therefore ask what planning would look like if the effect to detect were 100%, 75%, or 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so the corresponding planning figures require more participants per arm. This relationship is a general feature of power calculations, not evidence that any particular smaller effect is the true effect.

These sample-size illustrations use the posted effect estimates as inputs. They do not establish that the trial was designed around those estimates, nor do they demonstrate that a planned analysis was prespecified. The trial’s original design rationale, including any target effect or planned enrollment calculation, is not reported in the registry record. The calculations are best used to understand the scale of a future planning exercise under the listed assumptions, not to reinterpret the trial’s observed results.

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 = 0.055; treatment proportion p₁ = 0.096; average p̄ = 0.076.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3738 = 0.7327.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3727 = 0.3136.
4. n = (0.7327 + 0.3136)² / (0.0418)² = 626.5, rounded up to 627 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 <- 0.0546875                          # control proportion
p1 <- 0.0964912280701754                          # 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(1143896)
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 = 627 (80% power), 839 (90% power)
 75% of observed effect: n per arm = 1,044 (80% power), 1,397 (90% power)
 50% of observed effect: n per arm = 2,187 (80% power), 2,928 (90% power)
power.prop.test: 626.5 
Simulated power at n = 627 per arm: 0.811 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and two secondary outcomes, but it does not report a multiplicity procedure, a testing hierarchy, or a prespecified rule for interpreting the family of outcome tests. The record also reports no analyses in its analysis listing. It is therefore not reported in the registry record whether the secondary comparisons were intended as confirmatory tests, exploratory analyses, or both.

Multiplicity is the general issue that testing several outcomes can increase the probability of seeing at least one result that appears unusual by chance. Adjustments or prespecified hierarchies are possible ways to address that issue, but no such approach is described in the registry record. Consequently, the posted secondary p-values should be interpreted individually and cautiously, rather than as a set of definitive tests establishing an overall intervention effect. The primary comparison also should not be assumed to have been protected from selective analysis decisions when the analysis plan is not reported.

The primary population is labeled intent to treat. This indicates the stated analytic population, but the registry does not report the procedures used to manage missing outcomes, deviations from assigned care, or participants without endpoint information. The outcome denominators posted for the primary comparison differ by arm; the record does not explain whether those denominators reflect the full assigned groups, available endpoint data, or another analysis rule. No imputation method, sensitivity analysis, or missing-data assumption is reported in the registry record.

These reporting gaps do not show that analyses were mishandled. They mean that readers cannot assess from the registry record whether outcome selection, missing-data decisions, or multiplicity were handled according to a prespecified plan. The posted comparisons remain interpretable as unadjusted summaries, while stronger claims about the full analysis strategy require information that is not reported in the registry record.

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 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: death (irb determined unrelated to the study) (4.1%).

The registry posts serious adverse events for both trial arms. In depression collaborative care, 6 serious adverse events were recorded among 145 participants at risk; in usual care, 3 were recorded among 147 participants at risk. Other adverse events were recorded as 0 in each arm. The registry lists “Death (IRB determined unrelated to the study)” among the top serious-event terms, with 4.1%. That term is reported as an event description and is not assigned to an arm in the listed summary.

The record does not provide a separate death count, and the deaths field is null for both groups. The event figures should not be interpreted as a detailed comparison of cause, timing, severity beyond the serious-event classification, or relation to study treatment. A count of serious events also does not by itself establish a causal connection with an intervention. The registry’s description of the death term explicitly notes that it was determined unrelated to the study; other event-level causal assessments are not reported in the registry record.

These figures are descriptive safety information. The registry does not report a formal statistical comparison of adverse-event rates, definitions beyond the serious and other categories, or a fuller account of event ascertainment. Differences in the posted counts should therefore be read as recorded counts, not as proof of a safety difference between groups.

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

The primary result answers a narrow question: whether the proportion of participants recorded as initiating interferon treatment within 12 months differed between randomized groups. The observed proportion was higher in depression collaborative care, but the unadjusted risk-difference confidence interval includes zero and the unadjusted p-value is 0.216. The posted data therefore leave substantial uncertainty about the size and direction of the underlying difference.

The result does not establish that collaborative care increased antiviral treatment initiation, nor does it establish that the intervention had no effect. Failure to obtain a small p-value is not evidence that two approaches are equivalent. Establishing equivalence or ruling out an effect of a particular size requires a prespecified margin and an analysis designed for that purpose; neither is reported in the registry record. Likewise, a point estimate favoring one arm is not enough to conclude that the intervention caused a meaningful change.

The primary endpoint is treatment initiation, not treatment completion, virologic response, liver disease progression, quality of life, or depression symptom improvement. The posted results do not answer those broader clinical questions. The registry’s rationale describes the intended pathway from collaborative depression care to addressing barriers to antiviral treatment, but the primary endpoint alone cannot identify which part of that pathway affected the observed outcomes.

The secondary results concern care quality and medication adherence. They suggest a generally favorable pattern for the collaborative-care arm, with differing degrees of statistical precision, but they are not substitutes for the primary endpoint. They also require caution because multiplicity handling and the full analysis plan are not reported. The record supports describing the observed group summaries and their uncertainty; it does not support broad conclusions about all patients with hepatitis C and depression or about other settings and care models.

In general, clinical interpretation depends not only on whether an estimate differs from zero but also on the magnitude that matters to patients and clinicians, the outcome’s relevance, and the study’s limitations. The registry does not report a threshold for a clinically important difference. The most defensible reading is therefore descriptive: the observed initiation count favored collaborative care, while the interval remains broad enough that the true contrast is not precisely determined by these posted results.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a favorable point estimate and a precise estimate. The posted primary risk difference is positive, but its confidence interval includes no difference and extends to both negative and positive values. Looking only at the direction of the estimate would overstate what the observed data establish; looking only at the p-value would also obscure the range of effects that remain compatible with the data.

The endpoint is a concrete care-process outcome: receiving at least one interferon prescription during 12 months. That makes the primary comparison readily interpretable as treatment initiation, while also limiting the conclusions to initiation rather than later treatment outcomes. The secondary measures add information about other aspects of care, but their different results and the absence of reported multiplicity procedures show why a study’s outcomes should not be collapsed into a single broad claim.

The record also highlights the importance of analysis transparency. It identifies a randomized design and an intent-to-treat primary population, yet the detailed statistical plan, missing-data handling, and original sample-size assumptions are not reported in the registry record. This distinction matters: a registry can provide useful descriptions of the trial and posted outcomes without documenting every decision needed to reproduce or fully evaluate its analysis.

Finally, the planning illustrations demonstrate how power calculations depend on the effect chosen for planning. Smaller target effects call for larger per-arm planning figures under the stated assumptions. Those illustrations are not observed power and do not reveal the trial’s original design rationale. Together, the results and planning information encourage readers to focus on effect estimates, uncertainty, outcome definitions, and reporting limits rather than treating a single test result as a complete account of the evidence.

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 trial-specific limitations follow from the registry record. The study was unmasked, so participants and study personnel were not blinded according to the recorded design. The record does not describe how this might have affected care decisions or outcome ascertainment. The primary endpoint is a prescription-based initiation measure; it does not report whether participants took or completed treatment, and no broader clinical outcomes are included in the primary result.

The primary comparison is imprecise, with a confidence interval that spans negative and positive risk differences. The posted outcome denominators are not the same as the registry’s overall enrollment figure, and the record does not explain the relationship or describe missing endpoint data. Although the primary population is labeled intent to treat, specific handling of missing observations and deviations from assigned care is not reported in the registry record.

The analysis record is limited. No analyses are listed, and the statistical plan, adjustment variables, multiplicity methods, and original sample-size justification are not reported. The secondary comparisons are unadjusted recalculations, so their p-values should not be taken as definitive evidence across multiple outcomes. The record also does not report detailed participant characteristics, site information, eligibility criteria, or the full intervention protocol. Those omissions constrain assessment of how broadly the results might apply and how reproducible the intervention would be.

These are limits of what can be established from the registry record, not proof that the trial lacked procedures or that its conduct was flawed. They mean that interpretation should remain close to the posted outcome definitions and unadjusted summaries. More detailed reporting would be needed to assess the original analysis plan, missing-data assumptions, implementation, and generalizability.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Hepatitis C Translating Initiatives for Depression Into Effective Solutions — NCT01143896.
• Registry record last updated 2016-05-16; status last verified 2016-04.
• Results first posted 2016-04-11.
• 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 describes NCT01143896, “Hepatitis C Translating Initiatives for Depression Into Effective Solutions,” as a completed randomized, unmasked, parallel-group trial sponsored by the VA Office of Research and Development. Enrollment was 309. The study compared a depression collaborative-care model with usual care, which included depression screening without the collaborative-care team.

The primary endpoint was initiation of hepatitis C antiviral treatment within 12 months of enrollment, defined by receipt of at least one interferon prescription. The posted arm summaries show 11 initiations among 114 participants in collaborative care and 7 among 128 in usual care. The unadjusted risk difference is 0.042, with a 95% confidence interval from -0.025 to 0.109 and p = 0.216.

Two secondary outcomes concern quality of hepatitis C care and medication adherence. Their posted estimates generally favor collaborative care, but multiplicity procedures and detailed analysis methods are not reported in the registry record. The primary result is uncertain in direction and magnitude, and the registry record does not provide enough detail to assess missing-data handling or the original statistical plan.