Smoking Cessation Intervention for Women Living With HIV: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Smoking Cessation Intervention for Women Living With HIV (NCT02898597), a randomized na study. The primary outcome is Number of Participants With Abstinence.

2. Clinical Question

3. Trial Design

This was a completed, randomized, parallel-group pilot study of smoking cessation support for women living with HIV. The registry lists the allocation as randomized and masking as single. It does not specify who was masked, so the masking designation cannot be interpreted more narrowly from the record. The phase is listed as NA. The sponsor was the University of Massachusetts, Boston.

The intervention was cognitive behavioral therapy delivered by video call or by voice call. The posted primary outcome identifies the comparison arm as Telephone, while the arm description calls the format voice-call delivered therapy. The Video arm received video-call delivered therapy. The registry record does not describe randomization procedures, allocation concealment, treatment schedules, or whether participants could receive other smoking cessation support.

Enrollment is recorded as 49. For the primary outcome, the displayed group denominators are 21 for Video and 21 for Telephone. The record does not explain this difference, including whether it reflects exclusions, missing outcome data, or another analysis-population definition. No explanation should be inferred from the group counts alone.

The primary endpoint was assessed at 6-month follow-up and concerned self-reported abstinence since the quit day, with planned salivary cotinine verification at both 3-month and 6-month follow-ups. The registry lists the study as completed, with a start date of 2016-06-01 and primary completion date of 2017-12-01. It describes the work as a pilot to develop an intervention, but the original sample-size justification and other design assumptions are not reported in the registry 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: Women living with HIV

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: The women who are living with HIV.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Abstinence, measured over 6-month follow-up.

The primary endpoint counts participants who reported abstinence from smoking since their quit day at 6-month follow-up. The registry describes the outcome as self-reported and says it was to be verified with a salivary cotinine test at both 3-month and 6-month follow-ups. The posted result is a count of participants, rather than a continuous measure of smoking exposure or a time-to-event measure.

For this kind of endpoint, a count and its group denominator show how many participants met the stated outcome within each group. The posted counts are 8 of 21 for Video and 1 of 21 for Telephone. The registry record does not clarify whether all reported abstinence was confirmed by cotinine testing, how disagreements between self-report and testing were handled, or how participants without an assessment were classified.

Abstinence is relevant to a smoking cessation intervention because it directly describes the behavioral outcome the intervention aims to address. The record frames the study as a pilot to develop support for women living with HIV, not as evidence establishing effects for every setting or population. The endpoint description gives a target assessment and verification approach, but further operational definitions—such as how prolonged or interrupted abstinence was treated—are not reported in the registry record.

7. Results Posted in the Registry

• Telephone: 4.8% (1/21) versus 38.1% (8/21) on control; risk difference -33.3 percentage points (95% CI -56.0 to -10.7), risk ratio 0.12 (0.02–0.91); unadjusted two-proportion z-test p = 0.008.

8. Statistical Interpretation

9. Statistical Methods Explained

Different statistical methods summarize the same binary endpoint in different ways. The endpoint records whether each participant met the abstinence definition at follow-up, so a group count can be expressed as a risk, a risk difference, a risk ratio, or an odds ratio. Each measure answers a related but distinct question. The registry reports a logistic regression odds ratio and a Fisher Exact test; the unadjusted recalculation expresses the posted counts using several effect measures.

What does the risk difference describe?

A risk difference compares the proportion meeting the endpoint in one group with the proportion in another, preserving the difference on the probability scale. The recalculated risk difference is stated for Telephone relative to Video as -0.333, with an interval from -0.560 to -0.106. The negative direction indicates fewer observed abstinence outcomes in the Telephone group on this scale. The interval represents uncertainty around the estimated difference; values nearer to zero would indicate a smaller difference, while values farther from zero in the negative direction would indicate a larger difference in the same direction.

How do risk ratios and odds ratios differ?

A risk ratio compares the probability of the endpoint between groups as a ratio. The unadjusted recalculated risk ratio is 0.125, with an interval from 0.017 to 0.913. An odds ratio instead compares odds, where odds relate the chance of an event to the chance of no event. The unadjusted recalculated odds ratio is 0.081, with an interval from 0.009 to 0.728. Ratios below one in the stated Telephone-relative-to-Video comparison point in the direction of lower outcome frequency in Telephone. The odds ratio and risk ratio are not interchangeable, especially when interpreting their numerical size.

What does logistic regression contribute?

Logistic regression is a method for modelling a binary outcome through its odds. The sponsor reports a logistic regression odds ratio of 12.31, with a 95% confidence interval from 1.37 to 110.30 and p < 0.05, for the groups ordered Video and Telephone. The registry record does not report covariates, model specification, or whether the estimate is adjusted. The large width of the reported interval is important: the estimate’s direction is reported, but its magnitude is not precise. Because the recalculated unadjusted comparison differs from the sponsor analysis and the discrepancy flag is true, the sponsor’s own analysis takes precedence for reporting the sponsor result. The reason for the discrepancy is not reported in the registry record.

Why is Fisher’s Exact test reported?

Fisher’s Exact test evaluates evidence of an association between group assignment and a binary outcome using the observed counts. It is commonly used when group counts are small, because it does not rely on the same large-sample approximation used by some other tests. The registry reports p <0.05 for this test but gives no effect estimate or confidence interval alongside it. A p-value describes how compatible the observed data are with a specified null model; it does not measure the size of an effect, the probability that a hypothesis is true, or the importance of the outcome.

Why do counts and model results need context?

Counts are intuitive, but their interpretation depends on who was included in each denominator and how the endpoint was classified. The posted outcome denominators are 21 in each group, while the registry enrollment is 49. The record does not explain the difference. It also does not report how missing outcomes were handled, whether analysis followed randomized assignment, or whether cotinine verification was required for the posted endpoint. These details affect what population the estimates represent and how robust the comparison may be.

Randomization can support a comparison of assigned groups, but the registry’s designation alone does not resolve questions about adherence, missing data, outcome ascertainment, or analysis decisions. No adjustment method, prespecified analysis hierarchy, or interim analysis plan is reported in the registry record. A statistical result should therefore be read alongside the study’s pilot purpose, the limited posted analysis details, and the uncertainty expressed by the intervals.

10. Confidence Intervals and Precision

Precision concerns how narrowly an estimate identifies a range of values compatible with the data and analysis. The sponsor’s logistic regression estimate is an odds ratio of 12.31, with a 95% confidence interval from 1.37 to 110.30. The interval is wide, so the estimated magnitude is uncertain even though its reported limits are above the null value for an odds ratio. The p-value is reported as p < 0.05, but that threshold does not make the estimate precise.

The unadjusted recalculated risk difference for Telephone relative to Video is -0.333, with an interval from -0.560 to -0.106. The recalculated risk ratio is 0.125, with an interval from 0.017 to 0.913, and the recalculated odds ratio is 0.081, with an interval from 0.009 to 0.728. These estimates are based on the posted summary counts and are not the sponsor’s regression result. The reported discrepancy means the sponsor’s analysis takes precedence for the sponsor-reported finding.

Confidence intervals are ranges produced by a statistical procedure to represent uncertainty in an estimate under its assumptions. They are not guarantees that the true effect lies within the interval, and a wide interval can include substantially different effect magnitudes. Here, the limited outcome counts and the very wide sponsor interval counsel against treating a point estimate as an exact measure of the difference. The registry record does not report additional analyses that would clarify the discrepancy or improve interpretation of precision.

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 for 80% power and participants per arm for 90% power. They are not total sample sizes or observed participant counts. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect: 100%, 75%, or 50%.

For planning at 100% of the observed effect, the figures are 23 participants per arm for 80% power and 30 participants per arm for 90% power. For planning at 75% of the observed effect, they are 47 participants per arm for 80% power and 62 participants per arm for 90% power. For planning at 50% of the observed effect, they are 117 participants per arm for 80% power and 157 participants per arm for 90% power.

Power is the probability, under the planning assumptions and a specified true effect, that a study would meet its chosen statistical significance criterion. The 80% and 90% columns therefore describe different planning targets: the latter seeks a greater chance of detecting the assumed effect, and requires more participants per arm in these illustrations. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm.

These figures are planning illustrations calculated from the observed effect, not the trial’s original design assumptions; those original assumptions are not reported in the registry record. They are not observed power and do not show the probability that the posted result is true. They also do not establish what sample size would be appropriate under different endpoint definitions, follow-up procedures, or analysis methods.

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 = 0.381; treatment proportion p₁ = 0.048; average p̄ = 0.214.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5803 = 1.1373.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5303 = 0.4463.
4. n = (1.1373 + 0.4463)² / (-0.3333)² = 22.6, rounded up to 23 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 <- 0.380952380952381                          # control proportion
p1 <- 0.0476190476190476                          # 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(2898597)
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 = 23 (80% power), 30 (90% power)
 75% of observed effect: n per arm = 47 (80% power), 62 (90% power)
 50% of observed effect: n per arm = 117 (80% power), 157 (90% power)
power.prop.test: 22.6 
Simulated power at n = 23 per arm: 0.856 (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 reports two analyses comparing the Video and Telephone groups. The logistic regression result is an odds ratio of 12.31, with a 95% confidence interval from 1.37 to 110.30 and p < 0.05. The Fisher Exact result is p <0.05; no effect estimate or interval is reported for that test. The registry record does not describe the logistic model’s covariates or other specification details.

The unadjusted recalculation from the posted group counts gives a risk difference of -0.333 for Telephone relative to Video and an odds ratio of 0.081 on that same comparison orientation. Those figures do not agree with the sponsor’s reported logistic regression result as presented. The discrepancy flag is true, so the sponsor’s own analysis takes precedence when stating the sponsor-reported result. The registry record does not explain the difference, and the available details do not establish whether it reflects model specification, group coding, data handling, or another issue.

The sponsor analysis and the unadjusted recalculation should not be blended into a single estimate. The sponsor’s logistic regression is the reported model-based result; the recalculation is an unadjusted summary based on the posted counts. The wide sponsor confidence interval also signals substantial uncertainty in the reported effect magnitude. The registry record does not provide enough methodological detail to reconcile the analyses further.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and two analyses. The primary outcome is the number of participants with abstinence at 6-month follow-up. A logistic regression analysis and a Fisher Exact analysis are both reported for the Video and Telephone groups. The registry record does not state whether one analysis was designated as primary, whether they were planned as complementary analyses, or how their results were intended to be interpreted together.

Multiplicity arises when several outcomes, comparisons, or analyses are considered: the more opportunities there are to identify a statistically notable result, the more important it is to know whether and how the analysis plan accounted for that. The registry record does not report a multiplicity adjustment, an analysis hierarchy, or a prespecified plan for handling multiple analyses. It also lists no posted secondary outcomes. The absence of posted secondary results does not establish whether secondary outcomes were collected or considered.

Missing-data handling is not reported in the registry record. The enrollment figure is 49, while the posted primary outcome denominators are 21 in Video and 21 in Telephone. The record does not explain this difference or say whether any outcome observations were missing, excluded, or otherwise unavailable. It does not report an imputation method, a sensitivity analysis for missing outcomes, or the rule used to classify participants without an assessment.

The analysis population is also not described beyond the group counts. The record does not say whether participants were analysed according to randomized assignment, whether the posted groups include all randomized participants, or whether any participants were excluded after allocation. It does not report how treatment adherence or crossover was handled. These omissions limit the ability to assess whether the comparison preserves the benefits of randomization or how sensitive the result may be to outcome availability and analysis choices.

The endpoint description says abstinence was to be verified by salivary cotinine testing at 3-month and 6-month follow-ups. The registry record does not say how verification was incorporated into analysis or how self-report and testing were reconciled. These details are relevant to outcome classification, but should not be assumed from the endpoint wording alone.

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 2% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: kidney failure (4.2%).

The registry lists serious adverse event information separately for the safety groups. For Video, 25 were at risk for serious adverse events and 0 serious adverse events were recorded; 25 were at risk for other adverse events and 0 other adverse events were recorded; deaths were 0. For Telephone, 24 were at risk for serious adverse events and 1 serious adverse event was recorded; 24 were at risk for other adverse events and 0 other adverse events were recorded; deaths were 1.

The registry also lists Kidney failure as a top serious term at 4.2%. The record does not explain the relationship between that term and the group-level counts, nor does it provide further detail about timing, severity, attribution, or the clinical circumstances of the event. No causal relationship to an intervention should be inferred from these figures.

The safety denominators differ from the primary outcome denominators, and the registry record does not explain the difference. These are descriptive registry figures, not a complete assessment of comparative safety. The record does not report a statistical comparison of adverse events or deaths, and the sparse counts do not support a detailed estimate of relative risk. They should be read as recorded events in the listed groups, with the available context and limitations.

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

The posted results show more participants recorded as abstinent in the Video group than in the Telephone group at 6-month follow-up: 8 of 21 compared with 1 of 21. The unadjusted recalculation expresses that difference on several scales, while the sponsor’s analyses report a logistic regression odds ratio and a Fisher Exact p-value. The sponsor’s reported logistic result differs from the unadjusted recalculation, and the discrepancy flag means the sponsor’s own analysis takes precedence when describing its result.

This result does not establish that video-call delivery itself caused the observed difference. The registry record does not report enough detail about treatment content, adherence, missing outcomes, analysis population, or endpoint verification to rule out alternative explanations. It also does not explain why enrollment is 49 while the outcome denominators are 21 in each group. The posted counts are therefore best understood in the context of the specific analysis groups recorded.

The estimates are uncertain. In particular, the sponsor’s 95% confidence interval for the odds ratio, from 1.37 to 110.30, is wide. The unadjusted intervals also span a range of possible effect magnitudes. A statistically notable p-value does not make the magnitude precise, resolve the analysis discrepancy, or show the probability that the finding will recur.

The study is described as a pilot to develop a smoking cessation intervention for women living with HIV. Its result can inform understanding of this trial’s observed outcome and the planning illustrations based on that effect. The registry record does not establish how well the findings apply to other populations, care settings, intervention formats, or follow-up conditions. It also does not report a definitive clinical conclusion. The interpretation should remain limited to the recorded outcomes and analyses, with the uncertainty and missing methodological details kept in view.

17. Why This Trial Matters Statistically

This trial poses a practical statistical comparison: two delivery formats for cognitive behavioral therapy were evaluated for a binary smoking cessation endpoint in women living with HIV. The posted outcome is easy to understand as participant counts, but the analysis illustrates why counts alone are not the whole story. Effect measures describe the contrast on different scales, and confidence intervals show how uncertain those estimates remain.

The study also demonstrates the importance of keeping sponsor analyses distinct from unadjusted recalculations. The posted counts lead to an unadjusted comparison that differs from the sponsor’s logistic regression result. The record does not explain the discrepancy, so the two results should not be combined or treated as interchangeable. Reporting the difference plainly helps readers recognize that analysis choices and group coding can matter, while avoiding speculation about the reason.

Small outcome counts can produce imprecise estimates, as reflected in the sponsor’s wide confidence interval. A p-value below a conventional threshold does not remove that imprecision. The planning illustrations further show how assumptions about the effect worth detecting translate into different participant requirements: planning for a smaller fraction of the observed effect requires more participants per arm.

Finally, the record highlights the value of transparent reporting on denominators, missing data, endpoint verification, analysis populations, and multiplicity. The enrollment and outcome denominators differ, and the reason is not reported. The planned cotinine verification is described, but its role in the posted outcome is unclear. Such details are essential for evaluating what a trial estimate represents, especially in a pilot study intended to develop an intervention rather than settle every question about its effects.

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.

This trial’s interpretation is limited by the modest posted outcome counts and by the uncertainty reflected in the estimates. The sponsor’s logistic regression odds ratio has a wide 95% confidence interval, while the unadjusted recalculation does not match the sponsor analysis. The registry record does not explain the discrepancy, so its source cannot be identified from the available information.

The registry records enrollment as 49 but gives outcome denominators of 21 in each group and safety denominators of 25 for Video and 24 for Telephone. It does not report why those denominators differ or how participants were included in each analysis. Missing-data procedures, the analysis population, and sensitivity analyses are not reported. The endpoint description mentions planned cotinine testing, but the record does not clarify whether all posted abstinence outcomes were verified or how unverified or conflicting results were treated.

Additional trial details needed to assess the comparison are not reported in the registry record. These include the randomization procedure, allocation concealment, the identity of the masked party, treatment schedules, adherence, and the logistic model specification. The record also does not describe multiplicity procedures or identify a prespecified hierarchy for the two reported analyses. These absences do not establish that the procedures were not used; they mean the registry record does not report them.

The study is identified as a pilot, and its findings concern the recorded groups and endpoint. The registry record does not report the original sample-size justification, and the planning illustrations based on the observed effect do not resolve the uncertainty in the trial result. Generalization to other populations, intervention settings, or delivery formats is not established by the posted information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Smoking Cessation Intervention for Women Living With HIV — NCT02898597.
• Registry record last updated 2019-08-05; status last verified 2019-08.
• Results first posted 2019-08-05.
• 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

NCT02898597 is a completed randomized, single-masked, parallel-group pilot study sponsored by the University of Massachusetts, Boston. It compared cognitive behavioral therapy delivered by video call with therapy delivered by voice or telephone call for women living with HIV. Enrollment is recorded as 49.

The primary endpoint was the number of participants with self-reported abstinence since the quit day at 6-month follow-up, with salivary cotinine verification described for 3-month and 6-month follow-ups. The posted counts are 8 of 21 for Video and 1 of 21 for Telephone. The sponsor reports a logistic regression odds ratio of 12.31, with a 95% confidence interval from 1.37 to 110.30 and p < 0.05, and a Fisher Exact result of p <0.05. The unadjusted recalculation differs, so the sponsor’s own analysis takes precedence when describing its result. The registry record does not explain the discrepancy or the difference between enrollment and outcome denominators.