A Reinforcement Intervention for Increasing HIV Testing Among At-Risk Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Reinforcement Intervention for Increasing HIV Testing Among At-Risk Women (NCT03768986), a randomized na study. The primary outcome is Initial HIV Testing by Clients.

2. Clinical Question

This is a question about testing behavior, not an estimate of HIV infection or a clinical health outcome. Testing completion is relevant to the study’s stated aim because the registry summary describes knowledge of HIV status as important to linkage to care and broader HIV outcomes. The posted comparison concerns the intervention groups as defined in the record; it does not isolate reinforcement from every other possible difference in how community organizations operated. Information on provider-level variation, adherence to intervention procedures, and the exact eligibility rules is not reported in the registry record.

3. Trial Design

The registry identifies NCT03768986 as a completed, randomized, parallel-group behavioral study sponsored by UConn Health. The listed phase is NA. Masking is listed as none, so the record does not describe a masked trial. Enrollment is reported as 364. The study start date is 2019-02-04, and primary completion is dated 2024-12-11. These dates describe the registry record and do not establish when every participant completed follow-up.

The two posted treatment groups share standard referral for HIV testing and online HIV risk reduction training. Treatment Group B additionally received reinforcement; Treatment Group A did not. The registry summary describes partnerships with community-based organizations, including some that are not traditional HIV service providers, such as a domestic violence agency and a homeless shelter. The record’s broader stated purpose is to evaluate training community-based providers to deliver a reinforcement-based intervention for promoting HIV testing. Further details about provider training and intervention implementation are not reported in the registry record.

For the primary endpoint, the posted group sizes are 163 for Treatment Group A and 171 for Treatment Group B. The corresponding counts completing initial testing are 44 and 139. These are the denominators and event counts attached to the posted endpoint, while the registry separately reports overall enrollment of 364. The record does not explain the relationship between overall enrollment and the endpoint denominators, or describe participant flow, exclusions, or the number with missing endpoint information.

The registry lists six outcome measures and five analyses. The only secondary outcome identified in the record is satisfaction with training, measured with a single item. The full set of outcome definitions and results is not described in the available summary. The design details that would clarify randomization procedures, allocation concealment, protocol deviations, and the original statistical plan are not reported in the registry record. Consequently, the group comparison can be described from the posted results, but some features needed to assess conduct and analysis cannot be established.

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: 334 participants were assigned to the intervention group A or B 30 clinician participants were enrolled to deliver the intervention

Overall Study

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 Initial HIV Testing by Clients, measured over From date of intervention until 6 month testing reminders..

The primary endpoint is Initial HIV Testing by Clients, measured as the count of participants completing HIV testing after the initial intervention. Its stated timeframe runs from the date of intervention until six-month testing reminders. The registry description therefore concerns completion of initial testing within the stated intervention and reminder period; it is not a measure of repeat testing, HIV status, or subsequent linkage to care.

Testing completion is used because the study’s stated aim is to evaluate an intervention intended to increase HIV testing among women with risk factors for HIV. The registry summary explains that knowledge of HIV serostatus is relevant to linkage to care and HIV outcomes. That rationale gives the endpoint behavioral and public-health relevance, but the posted endpoint alone does not measure whether testing changed health outcomes or reduced transmission.

The outcome is reported as counts: 44 participants in Treatment Group A and 139 in Treatment Group B completed testing, with group denominators of 163 and 171, respectively. The registry also posts group proportions and comparative estimates for this endpoint. The precise rules for confirming test completion, handling an unverified test, and classifying participants without a recorded test are not reported in the registry record. The record does not state whether all participants were assessed at a common fixed visit; its timeframe refers to the intervention period and testing reminders. These details matter when interpreting what a recorded completion represents and how completely the endpoint was ascertained.

7. Results Posted in the Registry

• Treatment Group B: 81.3% (139/171) versus 27.0% (44/163) on control; risk difference 54.3 percentage points (95% CI 45.3 to 63.3), risk ratio 3.01 (2.32–3.92); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The posted comparison includes two related kinds of statistical information: the sponsor’s reported logistic-regression analysis and simple unadjusted recalculations based on the group counts and denominators. Keeping those distinct helps explain why estimates may share a label but reflect different analysis approaches. The recalculations describe the observed group summaries without adjustment for other variables. The sponsor’s reported method is logistic regression, and its posted effect measure is an odds ratio.

What does the risk difference express?

The risk difference compares the proportion with the endpoint in one group with the proportion in the other group. The posted estimate is 0.543, with an interval from 0.453 to 0.633. It is expressed on the probability scale, so it describes an absolute difference in the proportion completing testing. The two group proportions are 0.270 for Treatment Group A and 0.813 for Treatment Group B. The estimate is unadjusted and should be interpreted as a comparison of the posted group summaries, rather than as an estimate adjusted for participant or organization characteristics.

In general, an absolute comparison can be useful because it retains the outcome’s probability scale. It does not, on its own, identify why the groups differed or whether the estimate would be the same in another population or service setting. The registry does not describe adjustment variables for the sponsor’s regression or provide enough information to reconstruct that model.

How do the risk ratio and odds ratio differ?

The risk ratio compares the outcome proportions between groups. The posted risk ratio is 3.011, with an interval from 2.316 to 3.915. The odds ratio compares the odds of completion between groups, rather than the probabilities themselves. The sponsor reports a logistic-regression odds ratio of 11.75, and the unadjusted recalculation also gives an odds ratio of 11.75, with an interval from 7.005 to 19.7. The registry does not report an interval for the sponsor’s regression estimate.

In general, odds and probabilities are related but distinct scales. When an outcome occurs frequently, an odds ratio can be farther from the null value than the corresponding risk ratio. The odds ratio of 11.75 therefore should not be interpreted as participants being 11.75 times as likely to complete testing. The risk ratio and the risk difference offer complementary descriptions of the same posted comparison, while the odds ratio is the measure associated with the reported logistic-regression analysis.

What does the p-value tell the reader?

The unadjusted recalculation reports p < 0.001. The sponsor’s regression analysis reports p = .001. In general, a p-value describes how unusual data at least as discrepant as the observed data would be under a particular null hypothesis and analysis model. It does not give the probability that the null hypothesis is correct, and it is not a measure of effect size. The two reported formats should be retained as recorded; they should not be treated as exactly the same printed result.

Interpretation depends on the underlying analysis assumptions and on how the endpoint and analysis population were defined. The registry identifies logistic regression for the sponsor’s analysis but does not report model covariates, diagnostics, or a complete analysis specification. The recalculated comparison is unadjusted and uses the posted counts and denominators. Neither a small p-value nor a large odds ratio addresses the possibility of missing outcome information or systematic differences in implementation.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if the model does not account for that extra variability, which may in turn make confidence intervals too narrow and p-values too small. This is a general concept for count or clustered data, not a finding established for this endpoint. The primary outcome is reported as a binary event for each participant, and the registry does not report an over-dispersion assessment or a model that accounts for clustering within community organizations. Whether such features were relevant to the sponsor’s analysis is not reported in the registry record.

Randomization supports a planned comparison between groups, but it does not eliminate the need to understand how outcomes were recorded and analyzed. Details such as random sequence generation, concealment, adherence, handling of missing results, and whether the analysis followed assigned groups are not reported in the registry record. Those omissions limit the extent to which the posted estimates can be independently evaluated. The estimates remain interpretable as the group results and analysis statistics recorded, with the analysis details kept explicit.

10. Confidence Intervals and Precision

The interval for the unadjusted risk difference runs from 0.453 to 0.633. The posted interval for the risk ratio runs from 2.316 to 3.915, and the interval for the odds ratio runs from 7.005 to 19.7. These intervals communicate uncertainty around the corresponding estimates: in general, a confidence interval gives a range of values compatible with the observed data and the method’s assumptions. The confidence level used for these intervals is not reported in the registry record, so it should not be inferred.

The risk-difference interval is entirely above zero, and the relative-effect intervals are entirely above one. Those reference values represent no difference on the risk-difference scale and no relative difference on the ratio scales. In general, interval location and width help readers assess both direction and precision. They do not account for every uncertainty, such as uncertainty from missing data, imperfect endpoint measurement, or differences in intervention delivery that may not be represented in the statistical model.

The sponsor’s logistic-regression result is an odds ratio of 11.75, but its confidence interval is not reported in the registry record. The interval shown for the recalculated odds ratio is an unadjusted interval from the posted summary statistics and should not be presented as the sponsor’s regression interval. The two estimates have the same point value, but the record does not provide the sponsor’s interval or enough model detail for a fuller precision comparison.

Precision is also distinct from practical meaning. An estimate can be statistically precise under its calculation while still leaving uncertainty about implementation, measurement, and applicability beyond the study setting. The registry’s endpoint denominators and outcome counts give the basis for the posted unadjusted estimates, but participant flow and missing-data handling are not reported. Those omissions affect how completely the interval can represent the uncertainty relevant to the study as conducted.

11. 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 participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s own original design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning row uses the stated fraction of the observed effect to be detected. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the figures are 12 participants per arm for 80% power and 16 participants per arm for 90% power. At 75% of the observed effect, the figures are 23 participants per arm for 80% power and 30 participants per arm for 90% power. At 50% of the observed effect, the figures are 51 participants per arm for 80% power and 67 participants per arm for 90% power. The curve represents the same planning relationship across the effect assumptions.

In general, power is the chance that a specified statistical test would detect an effect of a stated size under the assumptions used for planning. The 80% and 90% columns therefore describe different target detection probabilities for hypothetical future study planning. A higher target power requires more participants under otherwise identical assumptions. A smaller effect also requires more participants to detect, which is why the listed per-arm figures increase as the assumed effect fraction becomes smaller.

These numbers are not observed power and do not describe the probability that the completed trial’s result is correct. They are planning illustrations calculated from the observed effect, and they do not replace the original trial design justification, which is not reported in the registry record. The observed group sizes are distinct from these hypothetical planning figures.

12. 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 = 0.270; treatment proportion p₁ = 0.813; average p̄ = 0.541.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7047 = 1.3811.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5909 = 0.4973.
4. n = (1.3811 + 0.4973)² / (0.5429)² = 12.0, rounded up to 12 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 <- 0.269938650306748                          # control proportion
p1 <- 0.812865497076023                          # 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(3768986)
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 = 12 (80% power), 16 (90% power)
 75% of observed effect: n per arm = 23 (80% power), 30 (90% power)
 50% of observed effect: n per arm = 51 (80% power), 67 (90% power)
power.prop.test: 12 
Simulated power at n = 12 per arm: 0.837 (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.

13. Analyses Reported by the Sponsor

The sponsor’s reported analysis uses logistic regression and gives an odds ratio of 11.75 with p = .001. The registry does not report a confidence interval for that estimate. The unadjusted recalculation from the posted group counts and denominators also gives an odds ratio of 11.75, with an interval from 7.005 to 19.7, and reports p < 0.001. The recalculation additionally reports the risk difference and risk ratio.

The two odds-ratio point estimates have the same displayed value, but the underlying methods are not identical: one is the sponsor’s logistic-regression result, while the recalculation is unadjusted and based on posted summary statistics. The registry does not give regression covariates or other details needed to characterize the sponsor’s model further. The sponsor’s p-value is reported as .001, while the recalculated p-value is reported as less than 0.001; those formats are presented as recorded rather than treated as interchangeable.

The discrepancy indicator is false, and no discrepancy requiring precedence is identified. The recalculation is useful as a transparent summary-based comparison, but it does not replace the sponsor’s analysis. The sponsor’s result remains the reported regression analysis; the recalculated estimates should be understood as complementary unadjusted calculations, not as a revision of the sponsor’s model or its inference.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and five analyses, and identifies satisfaction with training, measured with a single item, as a secondary outcome. The primary endpoint is initial HIV testing by clients. The registry does not report a multiplicity adjustment, a hierarchy of confirmatory outcomes, or a detailed plan for interpreting results across outcomes and analyses. It is therefore not possible to determine from the registry record whether or how the risk of false-positive findings across multiple tests was addressed.

In general, multiplicity arises when several outcomes, comparisons, or analyses are tested. The more opportunities there are to identify a nominally statistically significant result, the more important it is to understand whether testing was planned and whether any adjustment or prespecified hierarchy was used. This general concern does not establish that the reported primary result is invalid; it identifies information needed to assess the result in the context of all planned analyses. The results and definitions for all listed outcomes are not fully described in the available registry record.

Missing-data handling is not reported in the registry record. The record gives endpoint denominators of 163 and 171, while overall enrollment is 364, but does not explain participant flow, the status of participants without a posted endpoint result, or whether missing outcomes were excluded, imputed, or otherwise handled. It also does not report sensitivity analyses for missing endpoint data. As a result, the posted group proportions are interpretable as recorded, but the treatment of incomplete outcome information cannot be assessed.

The analysis population is not described in enough detail to establish whether participants were analyzed according to randomized assignment, whether any participants were excluded after randomization, or how protocol deviations were treated. The registry identifies the study as randomized but does not report allocation details or an intention-to-treat analysis statement. Interim analyses and stopping rules are not reported in the registry record. These missing details limit assessment of multiplicity control, missingness, and the relationship between the planned analysis population and the reported denominators.

15. 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 5% reporting threshold.

The registry’s serious adverse event figures list zero serious adverse events affecting participants in Treatment Group A and zero in Treatment Group B. The listed numbers at risk for serious adverse events are 163 and 171, respectively. The record also lists two deaths in Treatment Group A and zero in Treatment Group B; no deaths are listed for the clinician group. For other adverse events, the figures affecting participants are zero in both treatment groups, with zero listed for clinicians.

These are descriptive registry counts. The record does not provide serious adverse event terms, since no top serious terms are listed, and it does not describe the circumstances, timing, or relationship to study participation for the deaths. The clinician group has zero listed at risk for the adverse-event categories and is not a participant treatment arm. The figures should therefore be read as the counts recorded, not as a comparison adjusted for exposure time or a causal assessment.

In general, a count of zero in a registry entry does not establish that an event was impossible or that all events were captured under identical procedures. The registry does not report the adverse-event collection methods or additional safety-analysis details. The posted counts alone cannot establish whether an event was related to an intervention, and they should not be used to make an individual treatment decision.

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

The posted data show that initial HIV testing completion was recorded more often in Treatment Group B, which received standard referral, online HIV risk reduction training, and reinforcement, than in Treatment Group A, which received standard referral and online training. The counts are 139 of 171 in Treatment Group B and 44 of 163 in Treatment Group A. The unadjusted risk difference is 0.543, and the sponsor’s logistic-regression analysis reports an odds ratio of 11.75.

This result addresses testing completion over the endpoint timeframe described in the registry. It does not directly establish whether reinforcement alone caused the group difference, because the registry does not provide complete detail on implementation, provider variation, adherence, or the analysis population. Randomization is part of the recorded design, but the record does not report the procedures needed to assess how allocation was generated or concealed. The results should therefore be read as the posted comparison within this study, rather than as a universal prediction for other settings.

The primary endpoint is behavioral. It does not show whether participants who tested received follow-up care, whether repeat testing increased, whether HIV outcomes changed, or whether transmission was affected. The registry summary describes these broader issues as part of the motivation for the research, but the primary result reported is completion of initial HIV testing. No additional clinical effects should be inferred from that endpoint.

The estimates are statistically distinct from no difference under the reported analyses, with p < 0.001 for the unadjusted recalculation and p = .001 for the sponsor’s regression. Statistical evidence does not by itself establish practical importance, completeness of follow-up, or transportability. Interpretation also depends on how testing completion was verified and how missing information was handled; those procedures are not reported in the registry record. The result is informative about the posted endpoint and groups, while leaving those other questions unresolved.

17. Why This Trial Matters Statistically

This trial addresses an outcome that is often a necessary step in a broader care pathway: completion of HIV testing among women described in the registry as facing health disparities and risk factors for HIV. The study also emphasizes community-based organizations, including providers outside traditional HIV services. From a statistical perspective, that context makes it important to consider not only the overall group comparison but also how interventions are delivered across organizations and how testing completion is measured.

The posted result illustrates why effect measures should be read on their own scales. The risk difference of 0.543 describes an absolute contrast in the proportion completing testing; the risk ratio of 3.011 compares proportions; and the odds ratio of 11.75 compares odds. Because these measures answer related but different questions, placing them side by side can help readers avoid interpreting an odds ratio as a direct multiplier of probability. The interval estimates also communicate uncertainty that a point estimate alone cannot convey.

The comparison is statistically striking in the posted data, yet statistical strength does not fill gaps in reporting. Randomization is identified, but randomization procedures, missing-data handling, the analysis population, and the sponsor model details are not reported in the registry record. These are relevant to assessing how robustly the posted comparison represents the trial and how readily it can be generalized. The absence of these details is a limitation of the available record, not evidence that the procedures were inadequate.

Finally, the endpoint keeps the interpretation focused. A difference in initial testing completion is not the same as a difference in repeat testing, linkage to care, or health outcomes. Keeping the measured outcome distinct from the broader rationale is essential when translating a behavioral trial result into a statistical conclusion. The registry supports a description of the testing result, while several downstream questions remain outside the posted primary outcome.

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 details needed to evaluate the comparison are not reported in the registry record. These include participant eligibility criteria in operational detail, participant characteristics by group, the randomization sequence and concealment procedures, and the relationship between the overall enrollment of 364 and the primary endpoint denominators of 163 and 171. Without participant flow and reasons for any unavailable outcomes, the extent and handling of missing endpoint data cannot be determined.

The registry does not report how completion of an HIV test was verified, how testing was recorded across participating organizations, or whether the endpoint was assessed consistently. This matters because the primary comparison depends on the classification of a participant as having completed testing. Details of intervention fidelity, reinforcement delivery, and provider training are also not reported in enough detail to establish how consistently the two conditions were implemented across organizations.

The sponsor’s logistic-regression result is reported as an odds ratio of 11.75 and p = .001, but covariates, model diagnostics, and a confidence interval for that regression estimate are not reported. The unadjusted recalculation is based on posted summary counts and does not adjust for participant or organization characteristics. The registry does not report whether clustering by community organization was considered, whether missing-data sensitivity analyses were performed, or whether the reported analysis followed randomized assignment.

The registry lists six outcome measures and five analyses but does not report a complete multiplicity plan or the full results for every outcome. Interim analyses and stopping rules are not reported. The secondary outcome identified is satisfaction with training, measured with a single item; further measurement detail is not reported. These gaps limit assessment of the complete analysis context and of whether the primary result was interpreted within a prespecified hierarchy.

Finally, the trial’s stated population and community setting may not represent all people who could be at risk of HIV or all service settings. The record does not provide enough detail about enrolled participant characteristics or participating organizations to define the reach of the findings precisely. This limits generalizability claims without negating the description of the posted group results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Reinforcement Intervention for Increasing HIV Testing Among At-Risk Women — NCT03768986.
• Registry record last updated 2026-09-30; status last verified 2026-09.
• Results first posted 2026-09-30.
• 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

NCT03768986 is a completed randomized parallel-group behavioral study sponsored by UConn Health. It compares standard referral for HIV testing plus online HIV risk reduction training with the same services plus reinforcement among women described as at risk for HIV. The registry reports enrollment of 364 and identifies initial HIV testing by clients as the primary endpoint.

The posted endpoint counts are 44 of 163 in Treatment Group A and 139 of 171 in Treatment Group B. The unadjusted risk difference is 0.543, with an interval from 0.453 to 0.633. The sponsor reports a logistic-regression odds ratio of 11.75 and p = .001; the unadjusted recalculation reports p < 0.001. The registry does not report several details needed to assess missing data, analysis populations, multiplicity, and model specification. The primary result concerns initial testing completion and does not establish downstream clinical outcomes.