Feasibility of SBIRT-PN: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Feasibility of SBIRT-PN (NCT03057119), a randomized na study. The primary outcome is Number of Participants Ranking Intervention as Acceptable.

2. Clinical Question

The study addressed whether a Screening, Brief Intervention, and Referral to Treatment approach with peer navigation could be delivered and assessed among underserved HIV-positive adults aged 50 and older in primary care settings. Its framing is feasibility-focused: the registry describes substance use as a concern in this population and notes that findings from older adults generally had not been verified in older adults living with HIV. The record does not establish that the trial was designed to provide a definitive test of clinical benefit.

Random allocation is recorded, with a parallel-group model and single masking. The record does not identify who was masked. The central statistical question is therefore whether the posted feasibility and acceptability information can be interpreted clearly, and how much comparative evidence the results support. In particular, the primary outcome entries do not support a usable two-arm comparison, so they cannot establish a comparative effect of SBIRT-PN over treatment as usual.

3. Trial Design

The registry classifies the study as randomized, single-masked, and parallel-group, with enrollment of 86. Its status is completed. The record identifies Phase I as the pre-COVID-19 intervention and treatment-as-usual groups, and Phase II as a post-COVID-19 CAN pandemic telesurvey. These phases differ in what was delivered and what could be measured: the registry explicitly states that the telesurvey group did not receive an intervention or peer navigation and did not complete the acceptability measures used in Phase I.

The Phase I intervention was a behavioral program with peer navigation. Its listed components include psycho-educational content, a readiness assessment, goal-setting, identifying and prioritizing needs, and an explanation of peer navigation with session wrap-up. The intervention description also refers to discussion of substance use and its relationship to HIV and aging, feedback on screening scores, readiness to change, and motivational interviewing. The treatment-as-usual group received a screening-score handout and a referral-resource guide with a quick introduction. These descriptions indicate that the comparator was not simply an absence of information.

Outcome-specific denominators vary. For the primary endpoint, the registry lists Phase I group counts of 9 and 5, while the secondary treatment outcome and safety entries list 17 participants at risk in each Phase I group. The overall enrollment of 86 does not resolve these differences. The record does not explain the flow from enrollment to each outcome population, whether entries reflect different analysis sets, or why the primary entries use different counts.

The study phase is listed as not applicable. The registry does not report a detailed account of sequence generation, concealment, masking procedures, protocol deviations, or a statistical analysis plan. These omissions limit assessment of how randomization and analysis were implemented. The listed design features describe the broad structure, but do not answer those operational questions.

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

Analysis population for the primary outcome, as defined in the registry: CAN Pandemic Telesurvey arm of this study did not include an intervention or a peer navigation element, and therefore did not have include the acceptability measures as in Phase I.

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 Number of Participants Ranking Intervention as Acceptable, measured over 30 Days.

The primary endpoint is the number of participants ranking the intervention as acceptable, assessed at 30 days. The registry describes a 10-item acceptability questionnaire. It says the total score is obtained by summing item ratings and can range from 10, indicating low acceptability, to 50, indicating high acceptability. The stated criterion treats the intervention as acceptable if 80% of participants rate it 4 or higher on at least 80% of the scale items. The investigators also planned to examine questionnaire items separately to identify strengths and weaknesses.

Acceptability is useful in a feasibility study because it addresses whether participants find an intervention acceptable enough to engage with, rather than directly measuring substance-use change or a health outcome. It can identify practical barriers and inform whether further evaluation is warranted. It is not, by itself, evidence that the intervention changes substance use or improves health.

The registry lists primary outcome count values of 9 for the SBIRT intervention group and 5 for treatment as usual. However, it does not give a usable two-arm estimate for this endpoint, and the listed group counts differ from the safety and secondary-outcome denominators. The record does not clarify the denominator used to calculate the acceptability criterion or explain the relationship between the counts and questionnaire responses. Phase II had no acceptability measure because it did not include the intervention or peer navigation. Consequently, the primary entries should be read as limited descriptive information, not as a complete comparative evaluation of acceptability.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

For a binary outcome, each participant is classified according to whether the event occurred. The registry labels the outcomes as counts of participants with an event. For the secondary treatment outcome, the event is obtaining formal substance-use treatment by 6 months. The primary acceptability endpoint is also expressed as a participant count, but the record does not provide a usable comparative estimate for it.

What a risk difference describes

A risk difference compares the event proportions in two groups by subtracting one group’s proportion from the other. A value of 0.0 means the observed proportions are the same in the posted data. For formal treatment, the registry reports one event in each Phase I group, with 17 participants in each group, and a risk difference of 0.0. This is a description of the observed data, not proof that the underlying probabilities are identical.

What a confidence interval adds

A confidence interval represents uncertainty around an estimated effect. In general, a narrower interval indicates greater precision, while a wider interval indicates less precision. When an interval for a risk difference includes 0, the data are compatible with no difference as well as with effects in either direction represented by the interval. The posted interval for formal treatment extends both below and above 0. The small event count makes the estimate imprecise; it cannot rule out a range of potentially important differences. The confidence interval is not a guarantee that the true effect lies within its limits.

How to read the p-value

The unadjusted p-value for the formal-treatment comparison is 1.0. A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. A large p-value does not demonstrate equivalence. Here, it must be read alongside the equal observed counts and the imprecise interval.

Relative measures

The record also reports a risk ratio and an odds ratio for the formal-treatment comparison. A risk ratio compares event probabilities, while an odds ratio compares event odds. Both are relative measures and can appear especially unstable when the event is rare and the sample is small. Their confidence limits are broad in the registry entry. For this sparse result, the absolute counts and risk difference are more straightforward to interpret, while the relative measures should not be treated as precise estimates.

Why counts and denominators matter

Counts alone do not convey how common an event was unless the relevant denominator is also clear. The formal-treatment entry reports 1 event among 17 participants in each Phase I group. By contrast, the primary entries list counts of 9 and 5, and the safety entries list 17 at risk in each Phase I group. The registry does not reconcile these outcome-specific numbers. Analysts should not assume that the overall enrollment of 86 is the denominator for every endpoint, or infer a percentage when the endpoint population is unclear.

Planning calculations are not trial results

General sample-size planning asks how many participants might be needed to detect a specified effect under stated assumptions. The registry describes planning illustrations based on the observed effect, a two-sided significance level of 0.05, equal allocation, and a normal approximation. Such illustrations are hypothetical planning aids, not observed trial outcomes and not observed power. They do not show what the study was designed to detect unless the design assumptions and target effect were set prospectively and documented. The registry does not report a sample-size justification for the trial itself.

For a small feasibility study, planning from an observed effect is especially uncertain because the observed effect may be unstable. The primary comparison is not estimable, so it cannot anchor a comparative planning calculation in the same way as a complete primary estimate. Any planning value should therefore be understood as conditional on its assumptions, rather than evidence about the intervention’s effect or the adequacy of the completed study.

Finally, the registry lists no reported analyses for the secondary treatment outcome and does not report a detailed statistical analysis plan. The displayed risk difference, interval, and p-value should be understood as posted unadjusted results, not as evidence of adjustment for baseline differences or other covariates. The record does not state whether additional planned analyses were conducted or how missing observations were handled.

10. Exact Estimates for Each Arm

No two-arm comparison is shown for this trial, but each arm's result can still be summarized with exact interval estimates computed from the posted counts. The Clopper-Pearson interval is exact and conservative; the Wilson interval is a common closer-to-nominal alternative; the Bayesian credible interval uses a uniform Beta(1, 1) prior. For small groups the three can differ noticeably.

R code and output

arm    <- c("Phase I: SBIRT Intervention (Pre-COVID-19)", "Phase I: Treatment as Usual (Pre-COVID-19)")
n      <- c(9, 5)
events <- c(9, 5)
for (i in seq_along(n)) {
  ci <- binom.test(events[i], n[i])$conf.int          # Clopper-Pearson exact interval
  cr <- qbeta(c(0.025, 0.975), 1 + events[i], 1 + n[i] - events[i])   # Bayesian, uniform Beta(1,1) prior
  wi <- (function(x, n) { p <- x / n; z <- qnorm(0.975); d <- 1 + z^2 / n
    c((p + z^2 / (2 * n) - z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d, (p + z^2 / (2 * n) + z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d) })(events[i], n[i])
  cat(sprintf("ARM|%s|%d|%d|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f\n", arm[i], n[i], events[i], 100 * events[i] / n[i],
              100 * ci[1], 100 * ci[2], 100 * wi[1], 100 * wi[2], 100 * cr[1], 100 * cr[2]))
}

ARM  Phase I: SBIRT Intervention (Pre-COVID-19)  9  9  100.0  66.4  100.0  70.1  100.0  69.2  99.7
ARM  Phase I: Treatment as Usual (Pre-COVID-19)  5  5  100.0  47.8  100.0  56.6  100.0  54.1  99.6

11. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists three secondary outcomes. It does not report a multiplicity strategy, such as a prespecified ordering of tests, an adjustment to account for multiple comparisons, or a distinction between confirmatory and exploratory secondary analyses. When several endpoints are examined, the chance of finding at least one apparently unusual result can increase. This general concern is relevant to interpretation, but the record does not show whether multiplicity was considered in the investigators’ analysis plan.

The registry reports no analysis entries for the secondary treatment outcome and does not give a detailed statistical analysis plan. It does not state which analysis populations were intended, whether results were to follow an intention-to-treat principle, or how participants with missing outcome data were to be handled. Missing-data methods and the amount or pattern of missingness are not reported in the registry record. These omissions prevent assessment of whether the posted outcome counts represent all randomized participants, only those with available measurements, or another defined group.

Different outcome entries list different group sizes. The acceptability outcome has count entries of 9 and 5, while the formal-treatment outcome and safety entries list 17 participants at risk in each Phase I group. The record does not explain the differences. It is not possible to determine from the posted information whether this reflects missing questionnaire data, a separate analysis population, changes in enrollment, or another reporting issue. No explanation should be inferred.

The overall enrollment of 86 spans the study record, including the separate pandemic telesurvey phase, and cannot by itself define an analysis population for each endpoint. That later phase did not have an intervention or peer-navigation element and did not include the primary acceptability measures. The absence of a reported accounting of participants by phase and outcome limits assessment of both missingness and generalizability. These gaps are important for interpreting the sparse outcome results and for judging how much confidence to place in secondary comparisons.

12. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry safety entries list 17 participants at risk in each Phase I group and 52 in the Phase II CAN pandemic telesurvey group. Serious adverse events are recorded as 0 in all three groups, and other adverse events are also recorded as 0 in all three groups. The death counts are 1 for the Phase I SBIRT intervention group and 0 for the other two groups. These are descriptive registry entries; the record does not provide further detail about the death or its relationship, if any, to study participation.

Zero recorded adverse events does not establish that no events occurred outside the reporting scope or observation period. The registry does not describe the event-collection procedures, exposure time, or the level of detail used to classify events. The safety denominators also differ from the primary endpoint entries, which list counts of 9 and 5. The record does not explain the difference, so the safety population should not be assumed to match the primary endpoint population.

The study groups are small, and the posted safety counts are not a basis for a precise comparative safety estimate. A count in one group and none in another does not by itself establish a causal relationship. The Phase II telesurvey group is also not directly comparable to the intervention groups because it belongs to a distinct phase and did not receive the intervention. These figures should be read as registry-recorded counts, not as a complete assessment of safety or proof of absence of risk.

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

The results describe a completed randomized study whose stated focus was feasibility of SBIRT with peer navigation for underserved HIV-positive adults aged 50 and older in primary care. The record includes a primary acceptability measure, secondary service-use and substance-use outcomes, and safety counts. It also documents a change in study phase: the CAN pandemic telesurvey did not include the intervention or the acceptability assessment.

The primary outcome entries list counts of 9 for SBIRT and 5 for treatment as usual, but a two-arm comparison is not estimable from the posted data. The registry does not clarify the denominators behind those entries. The formal-treatment secondary result records one event in each Phase I group, with a risk difference of 0.0 and an unadjusted p-value of 1.0. Its uncertainty is substantial. The other substance-use outcomes do not have results detailed enough in the record to establish a common pattern.

These data do not demonstrate that SBIRT-PN is effective or ineffective. A missing or imprecise comparison is not evidence that groups are equivalent. Likewise, the acceptability counts cannot be translated into a comparative acceptability rate without a clear denominator and analysis. The posted figures do not establish whether the program changes substance use, increases formal treatment, or produces a particular safety profile.

The findings also do not settle whether the intervention is feasible in other settings or populations. The registry’s stated population is specific, and the record does not provide enough detail about participant characteristics, recruitment, adherence, or implementation to judge transferability. The distinction between Phase I and the later telesurvey phase further limits combining results across the full enrollment.

The most defensible conclusion is methodological: the registry contains limited descriptive outcome information, one sparse secondary comparison, and unresolved differences in outcome denominators. These features constrain the precision and scope of interpretation. Further claims about intervention effects, clinical importance, or population-wide consequences would go beyond what the posted results establish.

14. Why This Trial Matters Statistically

This trial matters statistically because it illustrates the difference between a feasibility question and an efficacy question. Acceptability can help assess whether an intervention is workable for participants, but it does not measure whether substance use changes. Keeping the primary question distinct from later service-use or substance-use outcomes prevents a secondary result from being mistaken for an answer to the primary aim.

It also shows why denominator clarity is essential. The primary entries list 9 and 5, while other Phase I entries list 17 participants per group. Without an explanation, readers cannot confidently determine which participants contributed to each outcome or calculate a comparable acceptability rate. Overall enrollment of 86 cannot resolve endpoint-specific populations, especially when the record includes a later phase with different activities and measures.

The formal-treatment result is another useful illustration of precision. Equal observed counts yield a risk difference of 0.0, but the confidence interval is broad and the event count is small. The point estimate alone can make a comparison look settled; uncertainty shows that the data remain compatible with effects in either direction. A p-value of 1.0 does not establish equivalence or rule out potentially meaningful effects.

Finally, the record highlights the importance of prospective statistical documentation. The registry does not report a sample-size justification, a detailed analysis plan, a missing-data approach, or a multiplicity strategy. Those details help readers distinguish planned analyses from exploratory findings and assess how robust conclusions may be. Their absence does not invalidate the recorded counts, but it limits the conclusions that can be drawn from them.

15. 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 are specific to the posted record. First, the primary acceptability outcome lacks a usable comparative estimate. Although the registry lists count values for both Phase I groups, it does not explain the relevant denominators or how the acceptability threshold was applied to those counts. This prevents a clear comparison of participant-level acceptability.

Second, the outcome-specific group sizes are not consistent across the record. The primary entries list 9 and 5, whereas the secondary treatment and safety entries list 17 participants in each Phase I arm. The registry does not explain whether these figures reflect different analysis populations, missing data, or another reporting feature. The discrepancy limits interpretation of the relationship between outcomes.

Third, secondary outcome reporting is incomplete. The registry lists self-reported and biologically confirmed substance-use outcomes, but does not provide comparable estimates for them in the posted results. The formal-treatment comparison is based on very few events, and its uncertainty is substantial. No multiplicity approach is reported, which further supports treating secondary findings cautiously.

Fourth, the study changed across phases. Phase II was a CAN pandemic telesurvey and did not include the intervention or peer navigation or the primary acceptability measures. The overall enrollment of 86 therefore should not be treated as a single homogeneous comparison population. The record does not fully describe participant flow through each phase and outcome.

Finally, protocol details that would support a fuller appraisal are not reported in the registry record, including the sample-size justification, detailed statistical analysis plan, handling of missing observations, and implementation information such as adherence. The masking description does not identify who was masked. These limitations constrain assessment of precision, risk of bias, and transferability.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Feasibility of SBIRT-PN — NCT03057119.
• Registry record last updated 2023-09-11; status last verified 2023-09.
• Results first posted 2023-09-11.
• 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.

19. Record Summary

The registry describes a completed, randomized, single-masked, parallel-group feasibility study of SBIRT with peer navigation for underserved HIV-positive adults aged 50 and older in primary care. Overall enrollment was 86. Phase I compared the SBIRT intervention with enhanced treatment as usual; Phase II was a later CAN pandemic telesurvey without the intervention or acceptability assessment.

The primary outcome was participant-rated intervention acceptability at 30 days. The registry lists count values of 9 and 5 for the Phase I groups, but no usable primary comparison. The formal-treatment secondary outcome at 6 months records one event in each Phase I group and an unadjusted risk difference of 0.0. Other substance-use outcome results are not sufficiently detailed to support a broad pattern. Safety entries record 0 serious adverse events and 0 other adverse events in each group, and death counts of 1, 0, and 0 across the listed groups.

Different denominators, sparse events, and limited analysis documentation constrain interpretation. The registry record does not report a detailed statistical plan, missing-data methods, or sample-size justification.