Social Media HIV Prevention Intervention for High Risk Rural Women: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Social Media HIV Prevention Intervention for High Risk Rural Women (NCT03456453), a randomized na study. The primary outcome is Facebook Enrollment.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked, parallel-group trial, with the NIDA Standard via Facebook compared with re-entry services as usual. Enrollment is listed as 60, and the record status is completed. The registry lists the phase as NA. It does not report who was masked, how the random sequence was generated, or the method used to conceal allocation.

The intervention arm received the NIDA Standard for HIV Prevention through Facebook. The comparator arm received standard re-entry services available in the community and through the criminal justice system. The broader study aim was to adapt and feasibility-test an evidence-based HIV prevention education approach for high-risk, underserved rural women in Appalachia. The registry also describes a motivation to explore social media as a way to increase access to prevention interventions.

The primary outcome was Facebook enrollment, measured as a participant count over a timeframe of 3 months. The primary outcome arm records list 29 participants for NIDA Standard via Facebook and 25 for re-entry services as usual. The posted results include 15 participants meeting the primary outcome in each arm. A secondary posted outcome counted participants with use of injected drugs over 3 months; its arm records list 27 and 23 participants, respectively. Reasons for the different denominators across outcomes are not reported in the registry record.

The study’s start date is 2019-05-29, and its primary completion date is 2022-04-26. Those registry dates describe the study record and do not establish when individual participants were enrolled or assessed. The registry does not report the trial’s original sample-size justification, detailed eligibility criteria, randomization procedures, or a full statistical analysis plan. No analysis entries are listed in the record.

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: Number of participants released from jail, thus eligible to accept the "friend" request from the Facebook profile. All participants who were released were eligible to accept the "friend" request then individuals randomized to the NIDA Standard via Facebook were sent an additional invite to the closed intervention group

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 Facebook Enrollment, measured over 3 months.

The primary endpoint, titled Facebook Enrollment, counts participants who were released from jail and accepted the friend request from the Facebook study profile. Its timeframe is 3 months. The registry describes all released participants as eligible to accept the request; it also says participants randomized to the Facebook intervention were sent an additional invitation. The details of that invitation are not fully reported in the registry record.

This endpoint is used to assess whether participants engage with the Facebook-based study profile after release. For a feasibility-focused intervention, uptake is an operational measure: it indicates whether the intended social-media contact was accepted, rather than whether a health outcome changed. A count of acceptances can help describe reach and engagement, but it does not by itself establish the quality or duration of participation, completion of educational content, or any effect on HIV-related behavior.

The endpoint is binary at the participant level in the posted comparison: each participant either met the stated enrollment criterion or did not. The registry reports counts and arm denominators, but does not report additional detail about the timing of acceptance within the 3-month period, verification procedures, or handling of participants whose release or Facebook contact status could not be established. Those details would help readers understand how the operational definition was applied.

7. Results Posted in the Registry

• Re-entry Services as Usual: 60.0% (15/25) versus 51.7% (15/29) on control; risk difference 8.3 percentage points (95% CI -18.2 to 34.7), risk ratio 1.16 (0.72–1.87); unadjusted two-proportion z-test p = 0.542.

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.

Number of Participants With Use of Injected Drugs

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Re-entry Services as Usual: 26.1% (6/23) versus 29.6% (8/27) on control; risk difference -3.5 percentage points (95% CI -28.4 to 21.3), risk ratio 0.88 (0.36–2.17); unadjusted two-proportion z-test p = 0.781.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Re-entry Services as Usual and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: the number of participants with use of injected drugs over 3 months. Its arm-specific counts and comparison estimate are presented with the other outcome results. In broad terms, the secondary comparison does not show a clear separation between the assigned groups, and its uncertainty is substantial. The direction of its estimate is not the same as the primary engagement estimate, but these outcomes measure different things and should not be expected to move together.

The primary outcome concerns acceptance of a Facebook study-profile request, an uptake measure. The secondary outcome concerns reported injected-drug use. A participant can engage with a prevention profile without an immediate or measurable change in drug-use behavior, and a behavioral outcome can vary for reasons not captured by an enrollment measure. The registry does not report a formal analysis of the relationship between profile acceptance and injected-drug use, so the outcomes should be interpreted separately rather than as a causal sequence.

The registry record lists no reported analyses. It does not say that the secondary outcome was part of a confirmatory testing hierarchy, or that an adjustment was made for testing more than one outcome. Without a stated hierarchy or multiplicity adjustment, an unadjusted secondary result carries less evidential weight than a prespecified primary result. This is a general caution: examining multiple outcomes increases the chance that at least one will appear notable by chance, while a single secondary result does not independently establish a treatment effect.

The secondary denominator differs from the primary denominator in each arm. The reason is not reported in the registry record, and the posted results do not explain whether it reflects missing observations, outcome-specific eligibility, or another process. That uncertainty matters when comparing endpoints and limits conclusions about how complete or comparable the outcome data were. The secondary measure adds information about a behavior relevant to the study’s prevention context, but it does not resolve the uncertainty in the primary finding or establish an effect on broader health outcomes.

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

• Number of Participants With Use of Injected Drugs

9. Statistical Interpretation

10. Statistical Methods Explained

The primary and secondary outcomes are counts of participants who met a stated criterion. Each comparison is therefore based on a binary outcome at the participant level: the outcome is either present or absent for each person whose data contribute to that analysis. The posted results express the between-arm contrast as a risk difference, the difference between the two observed proportions. The primary contrast is oriented as re-entry services as usual minus NIDA Standard via Facebook; the secondary comparison uses the same arm ordering.

What does a risk difference communicate?

In general, a risk difference describes an absolute contrast between proportions. A value of zero corresponds to equal proportions. A positive estimate means the proportion is higher in the arm placed first in the contrast; a negative estimate means it is lower. This measure can be read on the probability scale and does not require converting the result into a relative measure. Its interpretation depends on the event definition and the arm order, so both should be checked before describing the direction.

The registry also posts relative measures, including risk ratios and odds ratios, for each comparison. In general, a risk ratio compares the proportions directly, while an odds ratio compares the odds of the event. These measures answer related but different questions, and their numerical scales differ. When the outcome is not rare, an odds ratio should not be casually described as if it were a risk ratio. For clear communication, the absolute risk difference and the arm-specific event counts and denominators are useful alongside relative measures.

How should uncertainty be read?

A confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions. In general, a wide interval indicates limited precision: the data allow a range of possible effect sizes. If the interval includes zero for a risk difference, the data are compatible with no difference as well as with effects in either direction. This does not prove that the groups are identical. It indicates that the estimate does not pin down the direction or size precisely.

A p-value summarizes 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. The posted p-values are unadjusted. The registry record does not describe the test or model used to obtain them, so the calculation method and any adjustments beyond the posted summaries are not reported in the registry record.

Why can binary outcomes be imprecise?

General explanation: estimates from binary outcomes depend on both the event counts and the denominators. With limited observations, a small change in the number of events can shift the estimated proportion appreciably. This can result in broad confidence intervals, especially when the event is uncommon or when the denominators are modest. The intervals are therefore important for interpreting the posted point estimates; a point estimate alone can make an uncertain comparison look more definite than it is.

The primary outcome has 15 events in each arm, with denominators of 29 and 25. The secondary outcome has 8 events among 27 participants in the Facebook arm and 6 among 23 in the usual-services arm. These are the outcome-specific records; the registry does not explain why the denominators differ between outcomes. They should not be assumed to represent the same analysis population without further information.

What does randomization contribute?

In general, random assignment aims to make treatment groups comparable at the point of allocation, including with respect to factors that are measured and factors that are not measured. It does not guarantee that every observed characteristic will be balanced in a study, nor does it resolve missing outcome data or problems in outcome measurement. The registry identifies the allocation as randomized but does not report the sequence-generation method, allocation concealment, or details of implementation. It also identifies single masking but does not state who was masked.

The registry posts no analysis entries. Consequently, the analysis population, covariate adjustment, handling of departures from assigned treatment, and approach to missing observations are not reported in the registry record. Without those details, the arm-level counts and unadjusted comparisons can be described, but a more complete assessment of the prespecified analysis cannot be made. The registry also does not report whether outcome assessment procedures were standardized or whether acceptance was independently verified.

11. Confidence Intervals and Precision

The primary risk difference is 0.083, with a 95% confidence interval from -0.182 to 0.347. The interval includes zero, so the posted data are compatible with no difference in acceptance. They are also compatible with a lower acceptance proportion in the re-entry-services arm and with a higher proportion in that arm. The range is broad enough that the direction and size of the contrast remain uncertain.

In general, confidence intervals describe precision, not the probability that the true effect lies inside a particular interval after the data have been observed. A broad interval means the estimate is not sharply determined by the data under the method’s assumptions. For a risk difference, an interval extending across zero is consistent with both positive and negative contrasts. It should not be reduced to a simple claim of “no effect,” because meaningful differences in either direction may remain compatible with the observed results.

The secondary risk difference is -0.035, with a confidence interval from -0.284 to 0.213. This interval also includes zero and allows a range of possible differences in either direction. It provides limited precision about the association between assigned group and the injected-drug-use count.

The registry does not report the interval-estimation method or the analysis details behind the posted comparisons. The posted arm denominators are limited, and the interval widths reflect that the outcomes do not provide a highly precise estimate of between-arm differences. The intervals should be considered together with the event counts, outcome definitions, and absence of reported analysis details; they do not establish equivalence between groups.

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 give participants per arm, not a combined total and not total events. They illustrate the number of participants per arm under stated assumptions for detecting a chosen fraction of the observed effect. For the primary outcome, the illustration uses a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. The effect to detect is set at 100%, 75%, or 50% of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes a planning target under which a study with the stated assumptions would have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher probability target. In general, greater planned power requires more participants when other assumptions are held constant. The figures are design illustrations; they are not evidence about the probability that the completed trial detected an effect.

The planning amounts increase as the target effect is reduced from the full observed effect to a smaller fraction. Smaller effects are harder to distinguish from random variation, so detecting them generally requires more participants. For the primary endpoint, the posted figures range from 564 participants per arm for 80% power at 100% of the observed effect to 3,049 participants per arm for 90% power at 50% of the observed effect. These are planning illustrations based on the observed estimate, not observed power.

The full observed effect is an unstable basis for planning when the trial estimate is imprecise. A future design would need a clinically and operationally justified target effect, rather than relying only on the observed estimate. The registry does not report the original design assumptions, the intended target effect, or whether the study was designed to test a confirmatory hypothesis. The secondary-outcome planning figures are also illustrations based on its observed effect and the same stated general planning assumptions.

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 = 0.517; treatment proportion p₁ = 0.600; average p̄ = 0.559.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7022 = 1.3763.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6998 = 0.5890.
4. n = (1.3763 + 0.5890)² / (0.0828)² = 563.9, rounded up to 564 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 <- 0.517241379310345                          # control proportion
p1 <- 0.6                          # 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(3456453)
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 = 564 (80% power), 755 (90% power)
 75% of observed effect: n per arm = 1,008 (80% power), 1,349 (90% power)
 50% of observed effect: n per arm = 2,278 (80% power), 3,049 (90% power)
power.prop.test: 563.9 
Simulated power at n = 564 per arm: 0.800 (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 two outcome measures: Facebook enrollment as the primary outcome and participant count for use of injected drugs as a secondary outcome. It lists no analysis entries. A multiplicity plan, including any outcome hierarchy, adjustment for multiple comparisons, or distinction between confirmatory and exploratory tests, is not reported in the registry record. The posted p-values are unadjusted. They should therefore be read as individual comparisons, not as results adjusted to account for testing multiple outcomes.

In general, multiplicity matters when several hypotheses are tested because the chance of at least one apparently unusual result can increase as more comparisons are considered. Adjustments can be used to control that risk, but they may also affect precision and power. There is not enough registry information to determine whether any adjustment was prespecified or performed outside the posted entries. The record does not report a complete statistical analysis plan or the timing of any analysis decisions.

Missing-data methods are also not reported in the registry record. The primary-outcome denominators are 29 and 25, while the secondary-outcome denominators are 27 and 23. The record does not explain the difference, state how many observations were missing, or describe whether missingness was related to release, contact, outcome status, or assigned group. It also does not describe imputation, complete-case analysis, or sensitivity analyses. No specific missing-data mechanism can be inferred from the denominators alone.

The analysis populations are not defined in the registry record. It does not state whether the posted comparisons include everyone randomized, only participants with outcome data, or another population. The record does not describe how participants who did not receive or engage with the assigned intervention were handled in analysis. These omissions limit assessment of whether the posted results follow an intention-to-treat approach and how robust the comparisons are to missing outcomes or nonadherence.

These are reporting limitations, not proof that particular analyses or procedures were absent from the conduct of the study. The registry record does not establish whether additional methods were used elsewhere. In the absence of those details, interpretation should remain anchored to the posted counts, unadjusted comparisons, and their uncertainty.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: non-fatal overdose (7.4%).

The serious-event records list 2 serious adverse events among 27 participants at risk in the NIDA Standard via Facebook group and 0 among 23 at risk in the re-entry-services-as-usual group. The record lists 0 deaths in each group. The top serious-event term is Non-fatal overdose, listed at 7.4%. The registry does not provide further detail in these safety fields about event timing, event-level overlap, severity beyond the serious classification, or causal attribution.

These counts should be read descriptively. A difference in recorded serious-event counts does not by itself show that the intervention caused or prevented an event. The denominators are outcome-specific and are not identical to the primary-outcome denominators. The registry record does not explain how participants were considered at risk, how events were collected, or whether the listed term accounts for all serious events.

In general, sparse event counts provide limited precision for comparing safety between groups. Zero recorded events in a group does not establish that the underlying risk is zero. Likewise, a listed serious event is not evidence that the assigned intervention caused it. The registry does not report an inferential safety analysis or a formal comparison between arms.

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

The posted primary result concerns acceptance of a Facebook study-profile friend request among participants released from jail. The observed counts are similar in absolute number, while the denominators differ. The estimated risk difference is uncertain, and its confidence interval includes values on both sides of no difference. The result therefore does not establish a clear between-group difference in this specific uptake measure.

That finding should not be generalized to all aspects of the intervention. Acceptance is not the same as completing an education program, retaining information, reducing risk behavior, or preventing HIV. The registry lists injected-drug use as a secondary outcome, but the record does not establish a clear group difference for that outcome either. Neither measure directly reports HIV infection or an HIV-related clinical endpoint.

The record describes a study intended to adapt and feasibility-test prevention education and to examine the use of social media to improve access. The posted primary endpoint provides information about one part of that process: whether a friend request was accepted. It does not on its own establish feasibility across all required stages, acceptability to participants, intervention fidelity, reach among all eligible women, or the sustainability of the approach. The registry does not report broader feasibility criteria or their results.

Randomization is relevant to comparing assigned groups, but the registry does not describe key design and analysis details, including allocation procedures, masking identity, analysis populations, missing-data methods, and the statistical plan. The posted counts and unadjusted comparisons can be described, but a complete evaluation of bias and analysis choices is not possible from the registry record alone.

These results should not be interpreted as evidence that either approach works or fails as HIV prevention. They provide limited, uncertain information about the posted measures in this study. The population, service setting, intervention delivery, and narrow operational definition of the primary endpoint all matter when considering whether the findings apply beyond the participants and procedures described in the registry.

17. Why This Trial Matters Statistically

This trial is statistically informative because it separates an engagement outcome from a health or behavior outcome. Accepting a social-media contact is a measurable step in intervention delivery, but it is not interchangeable with a clinical endpoint. Defining the primary measure this way makes the question concrete while also setting a boundary on what the result can support.

The posted primary comparison illustrates why an estimate needs its uncertainty alongside it. The point estimate alone may suggest a direction, but the confidence interval includes no difference and a broad range of positive and negative contrasts. For clinical researchers, this is a reminder that an observed group difference is not a precise estimate simply because a number can be calculated from the counts. Interpretation depends on the interval, the denominator, and the meaning of the endpoint.

The record also highlights the importance of reporting operational details. The primary endpoint involves release from jail, eligibility to accept a request, and an additional invitation in the intervention arm. Clear descriptions of timing, invitation delivery, outcome ascertainment, and analysis populations would help readers distinguish access, exposure, and acceptance. Those details are not fully reported in the registry record.

Finally, the study’s stated feasibility aim and the posted statistical comparisons answer different kinds of questions. A feasibility study can inform whether procedures are workable and identify uncertainty for later research; it need not provide a definitive estimate of a health effect. Here, the registry does not report the original sample-size justification or a full analysis plan, and the posted estimates are imprecise. The record is therefore useful for understanding the outcome definitions and observed counts, while also illustrating why cautious reporting and transparent methods are essential.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to this trial affect interpretation. The primary outcome is an operational engagement measure: acceptance of a Facebook study-profile friend request. It does not capture whether participants saw or completed prevention content, how often they engaged, or whether knowledge or behavior changed. The registry does not report measures of those intermediate steps or any HIV clinical outcome.

The intervention and comparator differ in delivery context. One arm received the NIDA Standard through Facebook, while the other received usual re-entry services available in the community and through the criminal justice system. The content and consistency of usual services are not described in detail. The registry also indicates an additional invitation for the Facebook arm, but the full procedure is not reported. These limits make it difficult to evaluate the exact contrast in exposure and engagement.

The primary endpoint applies to participants released from jail, but the registry does not report how many were released and eligible, or the number who received or could access a friend request. The record does not explain the different denominators for the primary and secondary outcomes. It also does not report missing-data handling, outcome verification, detailed analysis populations, or a full statistical analysis plan.

The posted comparisons are uncertain, and the registry lists no reported analyses. The record does not identify who was masked or provide the method for generating and concealing the random assignment. The study’s original sample-size rationale and design assumptions are not reported. These omissions restrict assessment of precision planning, potential bias, and the extent to which the posted analyses follow prespecified procedures. They do not establish that procedures were inadequate; they identify information not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Social Media HIV Prevention Intervention for High Risk Rural Women — NCT03456453.
• Registry record last updated 2026-06-15; status last verified 2026-05.
• Results first posted 2023-05-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed randomized, single-masked, parallel-group study with enrollment listed as 60. The intervention was the NIDA Standard for HIV Prevention delivered via Facebook; the comparator was re-entry services as usual. The primary outcome counted participants accepting a Facebook study-profile friend request within 3 months. A secondary outcome counted participants with use of injected drugs over 3 months.

The posted primary comparison does not establish a clear difference between groups, and its confidence interval indicates substantial uncertainty. The secondary comparison is also uncertain. The record lists serious adverse-event counts and 0 deaths in each group, but does not report a formal safety comparison. No analysis entries are listed. Details about the original sample-size justification, missing-data methods, analysis populations, multiplicity procedures, and several design procedures are not reported in the registry record. The results are best understood as limited evidence about the posted engagement and behavior measures, not as a definitive assessment of HIV prevention effects.