Proactive Outreach for Smokers in VA Mental Health: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Proactive Outreach for Smokers in VA Mental Health (NCT01737281), a randomized na study. The primary outcome is Number of Participants With Cotinine-Validated Abstinence From Smoking.

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, parallel-group trial of proactive outreach versus usual care. The sponsor was the VA Office of Research and Development. The condition listed was smoking, and the trial enrolled 1938 participants. The registry lists the phase as NA. The reported start date was 2014-07-01, and the primary completion date was 2017-06-30.

The proactive outreach arm was a behavioral intervention consisting of 7 telephone counseling sessions and nicotine replacement therapy. The usual-care arm was described as usual smoking-cessation care from clinical staff. The study summary explains that VA smoking-cessation treatment typically depended on a health care provider visit, while the intervention used electronic medical record information to identify smokers with a mental health diagnosis and reach out to them proactively.

Allocation was randomized, the model was parallel, and masking was listed as none. The registry does not report the sequence-generation method, allocation concealment, or further details of how participants were assigned. It also does not report the trial's original sample-size justification or the assumptions used for its design. The planning illustration attached to the posted results is based on the observed effect and should not be confused with the trial's original design assumptions.

The primary outcome was cotinine-validated abstinence from smoking at 12 months. A secondary outcome was self-reported 7-day abstinence at 12 months. The registry reports no analyses in its analyses listing. Thus, the comparisons discussed in the posted results are unadjusted comparisons of the reported summary data; an adjusted or model-based analysis is 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

Analysis population for the primary outcome, as defined in the registry: Cotinine samples were obtained by mail from 53/76 people reporting abstinence in the intervention arm and 44/58 people reporting abstinence in the control arm. Note that this reflects a "complete case analysis", only including people for whom outcome data are available.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Cotinine-Validated Abstinence From Smoking, measured over 12 months.

The primary endpoint was the number of participants with cotinine-validated abstinence from smoking at 12 months. Cotinine is used as a biochemical marker to check abstinence reported by participants. As a general measurement principle, biochemical validation can add information beyond self-report alone, although it does not eliminate limitations caused by incomplete outcome collection.

For this outcome, the registry says cotinine samples were obtained by mail from 53/76 people reporting abstinence in the intervention arm and 44/58 people reporting abstinence in the control arm. The posted primary comparison uses the people for whom outcome data were available: 36 of 53 in proactive outreach and 30 of 44 in usual care were recorded as abstinent. The registry explicitly characterizes this as a complete case analysis.

This endpoint therefore concerns validated abstinence among the participants with cotinine outcome data, not every person enrolled in the trial. Cotinine validation is relevant because the outcome is smoking abstinence, while the incomplete collection of samples means the result must be interpreted with attention to who had an observed outcome. The registry does not report further details about the validation procedure or the handling of missing cotinine results.

7. Results Posted in the Registry

• Proactive Outreach: 67.9% (36/53) versus 68.2% (30/44) on control; risk difference -0.3 percentage points (95% CI -18.9 to 18.4), risk ratio 1.00 (0.76–1.31); unadjusted two-proportion z-test p = 0.978.

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 Self-Reporting 7-Day Abstinence From Cigarettes

• 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:
  • Proactive Outreach: 19.2% (119/620) versus 13.7% (96/701) on control; risk difference 5.5 percentage points (95% CI 1.5 to 9.5), risk ratio 1.40 (1.10–1.79); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Proactive Outreach than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry reports one secondary endpoint: self-reported 7-day abstinence from cigarettes at 12 months. Its pattern differs from the primary endpoint in that the unadjusted secondary comparison has a positive risk-difference estimate and an interval that does not include zero, while the cotinine-validated primary estimate is close to zero with a broad interval spanning both directions.

These results concern related but non-identical measures. The primary endpoint required cotinine validation and was analyzed among people with available cotinine outcome data. The secondary endpoint relied on self-report and has different reported denominators. Differences in outcome definition, collection, and analysis population can contribute to differing estimates. The registry does not provide enough detail to determine why the results differ, or to assess the impact of missing outcomes on either comparison.

The secondary finding should be read alongside, not in place of, the primary result. It can add information about the self-reported outcome, but it does not establish the result for biochemical validation. The registry reports an unadjusted p-value for this secondary comparison and does not describe any correction for multiple outcomes or analyses. As a general statistical concern, evaluating multiple outcomes without adjustment can increase the chance of at least one apparently notable result arising by chance. The registry lists two outcome measures and one posted secondary outcome, while its analyses listing contains no reported analyses.

Accordingly, the secondary result carries less confirmatory weight than a primary result interpreted under a prespecified analysis plan. The registry record does not report the multiplicity strategy, whether the secondary endpoint was confirmatory or exploratory, or whether other analyses were conducted. The overall pattern is therefore one of a positive unadjusted self-report comparison alongside an imprecise primary validation comparison, with important differences in how the outcomes were measured.

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

• Number of Participants Self-Reporting 7-Day Abstinence From Cigarettes

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

As a general statistical concept, a risk difference compares the proportion with an outcome in one group with the proportion in another. A value near zero means the observed proportions are close. The sign indicates the direction of the comparison, provided the group order is kept clear. For the primary comparison, the reported risk difference is -0.003 for proactive outreach relative to usual care. The posted proportions, 0.679 and 0.682 respectively, are close, which corresponds to that small negative estimate.

A risk difference is an absolute measure: it expresses the difference on the outcome-proportion scale. It is distinct from a relative risk or an odds ratio, which compare groups using ratios. The reported primary relative risk was 0.996 and the reported odds ratio was 0.988. Those estimates are also near the value that represents no group difference for their respective measures. Measures can tell the same broad story while expressing the contrast on different scales. They are not interchangeable, and none resolves limitations in the underlying outcome data.

What does an interval communicate?

As a general statistical concept, a confidence interval conveys uncertainty around an estimated effect under the assumptions of the analysis. A narrower interval indicates greater precision; a wider interval indicates less precision. For the primary risk difference, the reported interval runs from -0.189 to 0.184. It contains zero and spans values on both sides of zero. That means the point estimate alone should not be read as a precise estimate of the direction or size of the group difference. The registry record does not state the confidence level for the displayed intervals, so no particular confidence percentage should be assumed from this description.

How should the p-value be read?

As a general concept, a p-value describes how unusual results at least as incompatible with a specified null hypothesis would be under the statistical model if that null hypothesis held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The posted primary unadjusted p-value is 0.978. Read alongside the small point estimate and broad interval, it indicates that the comparison does not provide evidence against a no-difference null under that unadjusted calculation. It does not prove the groups are equivalent.

The registry reports the secondary unadjusted p-value as 0.007. That value applies to the self-reported outcome comparison, not the cotinine-validated primary endpoint. The record does not report a multiplicity adjustment. When multiple outcomes are examined, unadjusted p-values do not account for the increased opportunity to observe a small p-value by chance across the set of analyses. That is one reason to interpret the secondary finding with more caution than a single confirmatory primary analysis.

Why do the outcome counts matter?

The primary endpoint is a count of participants with validated abstinence, and the comparison uses participants with outcome data. The registry states that cotinine samples were mailed to a subset of people who reported abstinence and identifies the primary comparison as a complete case analysis. This distinction matters: the denominator in an outcome comparison is the number with an observed outcome for that measure, not automatically the trial enrollment. Missing outcome data can affect precision and, depending on how missingness relates to outcomes or group assignment, can also affect the interpretation of a comparison. The registry does not report a missing-data model or sensitivity analysis.

The secondary outcome is self-reported 7-day abstinence. Its reported denominators are 620 in proactive outreach and 701 in usual care, with 119 and 96 participants reporting abstinence, respectively. This outcome has more reported observations than the cotinine-validated endpoint, but a larger denominator does not make the measures identical. Self-report and biochemical validation capture abstinence in different ways, and the registry does not explain the relationship between all analysis populations in detail.

What does randomization contribute?

As a general design principle, random allocation is intended to make treatment groups comparable on average with respect to both measured and unmeasured baseline characteristics. It supports a causal comparison when allocation and follow-up are implemented appropriately and when the analysis preserves the randomized comparison. The registry lists randomized allocation, but does not report the allocation procedure, a baseline balance analysis, or the specific analysis population used beyond the primary complete case description. Randomization alone does not ensure that missing outcomes are harmless, nor does it establish that every reported comparison is adjusted for the design.

The posted comparison is unadjusted. An unadjusted estimate compares the observed outcome summaries without a reported covariate adjustment. This is a direct and interpretable summary, but the registry provides no adjusted result to compare against it. It also reports no analyses in its analyses listing. Consequently, the record does not establish whether other modeling approaches were planned or whether other analyses were conducted outside the posted registry results.

What is the role of the planning illustrations?

As a general concept, power is the probability that a statistical test will reject a specified null hypothesis under a particular assumed effect and analysis setup. Planning calculations use assumptions about the effect to detect, significance level, allocation, and statistical method. The posted planning assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use stated fractions of the observed effect. These are planning illustrations based on the observed results, not evidence about the trial's original design or its achieved power.

In general, smaller effects are harder to distinguish from random variation and therefore require more participants under otherwise comparable assumptions. Such sample-size calculations depend on the chosen effect and model assumptions. They should not be read as a guarantee that a future study will achieve a particular result. The trial's original sample-size justification, design effect assumption, and any other original planning assumptions are not reported in the registry record.

Why can over-dispersion matter?

As a general statistical concept, over-dispersion means that the observed variability exceeds what a chosen model expects. It matters for outcomes analyzed with models that make assumptions about variance, because an underestimated variance can make uncertainty appear too small. This trial's posted primary outcome is a binary participant count, and the registry does not report an over-dispersion parameter or a model-based analysis. There is therefore no reported over-dispersion estimate to interpret for these results.

11. Confidence Intervals and Precision

The primary risk-difference estimate was -0.003, with a reported interval from -0.189 to 0.184. The interval crosses zero and extends in both directions. In plain terms, the point estimate is close to no difference, but the interval leaves substantial uncertainty about the magnitude and direction of the underlying difference. The posted result is therefore not precise enough to support a narrow conclusion about the primary outcome.

The relative-risk interval, 0.758 to 1.31, and the odds-ratio interval, 0.419 to 2.329, also include the value representing no group difference for those measures. These ranges are broad, especially for the odds ratio, and show that multiple effect sizes remain compatible with the observed summary data. The unadjusted p-value of 0.978 is consistent with the absence of a clear statistical separation in this comparison, but it does not demonstrate equivalence.

As a general principle, interval width depends on the amount of information and the variability of the outcome. The primary analysis included 53 participants in proactive outreach and 44 in usual care, with cotinine results available for a subset of people reporting abstinence. This limited outcome information contributes to uncertainty. The interval's confidence level is not stated in the registry record, so its coverage level should not be inferred. The interval also does not account for any unreported missing-data sensitivity analysis or model adjustment.

The secondary self-reported comparison has a narrower reported risk-difference interval, from 0.015 to 0.095, but it measures a different outcome and has different reported denominators. Its greater precision does not directly transfer to the primary endpoint. Precision must be evaluated for the specific endpoint and analysis population under discussion.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. The registry's planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each planning illustration is the stated fraction of the observed effect. The registry does not report the trial's original design assumptions or sample-size justification.

For the primary cotinine-validated outcome, planning for 100% of the observed effect gives 515,546 participants per arm for 80% power and 690,170 participants per arm for 90% power. Planning for 75% of the observed effect gives 916,038 participants per arm for 80% power and 1,226,314 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,059,981 participants per arm for 80% power and 2,757,729 participants per arm for 90% power.

In plain language, the 80% power column gives the estimated participants per arm under the stated assumptions for a design with an 80% chance of detecting the assumed effect at the stated significance level. The 90% column uses the corresponding 90% chance. The lower assumed effect fractions lead to larger planning estimates: smaller effects are harder to distinguish from random variation and require more participants under otherwise similar assumptions.

These calculations are illustrations based on the observed effect, not observed power. They are not a report of the power achieved by the completed trial, and they do not recover the trial's original design rationale. The unusually large primary planning figures reflect the very small observed risk difference used as the basis for the calculation; they should be interpreted as conditional planning results, not as a recommendation for a future study.

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 = 0.682; treatment proportion p₁ = 0.679; average p̄ = 0.681.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6594 = 1.2924.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6594 = 0.5550.
4. n = (1.2924 + 0.5550)² / (-0.0026)² = 515,545.9, rounded up to 515,546 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 <- 0.681818181818182                          # control proportion
p1 <- 0.679245283018868                          # 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(1737281)
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 = 515,546 (80% power), 690,170 (90% power)
 75% of observed effect: n per arm = 916,038 (80% power), 1,226,314 (90% power)
 50% of observed effect: n per arm = 2,059,981 (80% power), 2,757,729 (90% power)
power.prop.test: 515545.9 
Simulated power at n = 515,546 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 a primary endpoint and one secondary endpoint, and its outcome-measure count is 2. The secondary measure is self-reported 7-day abstinence at 12 months. The record lists no reported analyses and does not describe a multiplicity adjustment, a hierarchy for testing outcomes, or which secondary analyses, if any, were designated as confirmatory. Without that information, the secondary unadjusted p-value should not be interpreted as though it were the result of a single isolated test.

As a general statistical principle, multiplicity arises when several outcomes, comparisons, subgroups, or analyses are examined. If each is assessed without accounting for the others, the chance of finding at least one nominally small p-value can increase. Adjustments or prespecified testing hierarchies can address this concern, but the approach used for this trial is not reported in the registry record. The posted secondary comparison should therefore be treated as supportive or exploratory evidence rather than as an independently definitive result.

Missing outcome data are especially relevant to the primary analysis. The registry reports that cotinine samples were obtained by mail from 53/76 people reporting abstinence in proactive outreach and 44/58 people reporting abstinence in usual care. It explicitly describes the primary outcome comparison as a complete case analysis, using the 53 and 44 participants with outcome data. A complete case analysis excludes people without an observed value for that endpoint.

As a general concern, a complete case result can be affected if having an observed outcome is related to the outcome itself or differs in a consequential way between groups. The registry does not report a missing-data model, imputation, sensitivity analysis, or the assumptions used to address unavailable cotinine results. It also does not report further details about missing data for the secondary endpoint. The impact of missingness on the estimates cannot be determined from the posted information alone.

The registry does not report an intention-to-treat analysis, per-protocol analysis, adjusted analysis, or interim analysis. This does not establish that none occurred outside the registry record; their status and methods are not reported in the registry record. The trial's original analysis plan and sample-size justification are also not reported. These gaps limit assessment of whether the posted analyses match the originally planned analysis strategy.

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.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: hospitalization (4.0%), life-threating event (0.1%).

The registry reports serious adverse event figures for an intervention arm and a control arm, with 969 at risk in each. The serious-affect counts were 39 in the intervention arm and 28 in the control arm. Other-affect counts were 0 in each arm. Death counts were 9 in the intervention arm and 12 in the control arm. These are descriptive registry figures and do not establish that the intervention caused or prevented any event.

The registry lists hospitalization at 4.0% and life-threating event at 0.1% among the leading serious-event terms. The record does not specify the arm-specific distribution of those terms in the information reported for this comparison. The term is reproduced as entered in the registry.

Safety counts require context about definitions, event collection, attribution, timing, and whether a participant could contribute more than one event. Those details are not reported in the registry record. The counts should therefore be read as reported event summaries, not as adjusted comparisons of safety risk. The trial summary and posted safety figures do not provide a basis for medical advice or for attributing individual events to a study arm.

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

The primary posted comparison concerns cotinine-validated abstinence at 12 months among participants with available cotinine outcome data. The risk-difference estimate is close to zero, and its interval includes zero while spanning values in both directions. The posted data therefore do not precisely establish the direction or magnitude of a difference in this primary outcome. They also do not demonstrate equivalence between the groups.

The secondary outcome tells a different descriptive story: self-reported 7-day abstinence has a positive unadjusted risk-difference estimate and an interval that excludes zero. Because this measure is based on self-report rather than cotinine validation and has different denominators, it is not a substitute for the primary outcome. Its unadjusted result also needs caution because the registry does not report a multiplicity strategy.

The trial was randomized, which supports a comparative interpretation in principle. However, the primary result is a complete case analysis, and the registry does not report a missing-data sensitivity analysis or adjusted model. The reported outcomes alone cannot establish whether incomplete cotinine collection changed the comparison. The record also does not report the original sample-size rationale, detailed statistical plan, or further information needed to assess the full analysis process.

The results describe what was recorded for this trial and its stated outcomes. They do not establish why the primary and secondary estimates differ, demonstrate that either outcome captures every relevant aspect of smoking behavior, or establish what would occur in other settings. The trial summary discusses proactive outreach as an approach intended to reach smokers with a mental health diagnosis, but the posted estimates should be interpreted within the outcome definitions, analysis populations, and uncertainty reported.

Neither an unadjusted p-value nor a planning calculation determines clinical importance. The primary point estimate is close to zero, but the interval is broad; the secondary estimate is more clearly separated from zero in its unadjusted comparison, but it is a different endpoint. Readers should keep the distinction between the endpoint measurements and their uncertainty in view rather than treating one result as a complete account of the trial.

17. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between an outcome that is self-reported and one that receives biochemical validation. The primary endpoint is cotinine-validated abstinence, while the secondary endpoint is self-reported 7-day abstinence. The estimates differ in their observed pattern, but they also differ in measurement and reported analysis denominators. Interpreting them together requires attention to those design features, rather than assuming they are duplicate measurements of the same endpoint.

The primary comparison illustrates why an estimate and its precision must be considered together. Its point estimate is near zero, but the interval is broad and extends in both directions. A near-zero estimate with substantial uncertainty is not evidence of equivalence. The secondary comparison has a more clearly positive unadjusted estimate, but its interpretation is tempered by its secondary status and the unreported multiplicity strategy.

Missing outcomes also matter to the inference. Cotinine samples were not available for all people who reported abstinence, and the registry identifies the primary result as complete case. The missing-data mechanism and any sensitivity analysis are not reported. This makes transparent reporting of outcome collection and analysis populations particularly important when validated outcomes are collected from only some participants.

Finally, the planning illustration shows how sample-size requirements depend on the effect assumed for planning. The calculations use fractions of the observed effect, so planning for a smaller effect yields larger participant requirements. These are not a substitute for the original trial design justification or an estimate of achieved power. Taken together, the record is a reminder to distinguish primary from secondary results, validation from self-report, observed estimates from planning exercises, and absence of a clear statistical difference from evidence of no difference.

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.

A central limitation for interpreting the primary result is incomplete cotinine collection. The registry reports mailed samples from 53/76 people reporting abstinence in proactive outreach and 44/58 in usual care, and calls the primary comparison a complete case analysis. Without a reported missing-data model or sensitivity analysis, the influence of unavailable samples on the estimate is uncertain.

The primary comparison is based on relatively limited outcome counts compared with the trial enrollment, which is reflected in its broad interval. The registry does not state the interval confidence level, so its exact coverage cannot be assessed from the record. It also does not report an adjusted analysis or additional modeling details for the comparison.

The secondary self-reported outcome differs from the validated primary endpoint in how abstinence was measured and in its reported analysis denominators. Its unadjusted result does not resolve the uncertainty in the primary comparison. No multiplicity adjustment or testing hierarchy is reported, limiting the confirmatory interpretation of a secondary p-value.

Further details that would help assess the analysis are not reported in the registry record, including the original sample-size justification, detailed statistical analysis plan, allocation procedure, handling of missing secondary outcomes, and any sensitivity analyses. The registry lists masking as none, and does not provide additional information on how outcome reporting or assessment was managed in light of that design. These limitations describe gaps in the posted record; they do not establish that other procedures or analyses were absent outside the registry.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Proactive Outreach for Smokers in VA Mental Health — NCT01737281.
• Registry record last updated 2019-03-26; status last verified 2019-03.
• Results first posted 2019-03-14.
• 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

NCT01737281, titled Proactive Outreach for Smokers in VA Mental Health, is listed as a completed randomized, parallel-group trial with no masking. The sponsor was the VA Office of Research and Development. Enrollment was 1938, and the listed dates were 2014-07-01 for study start and 2017-06-30 for primary completion.

The trial compared proactive outreach, consisting of 7 telephone counseling sessions and nicotine replacement therapy, with usual smoking-cessation care from clinical staff. The primary endpoint was cotinine-validated abstinence at 12 months. Its unadjusted risk difference was -0.003, with a reported interval from -0.189 to 0.184 and p = 0.978. The secondary endpoint was self-reported 7-day abstinence at 12 months, with an unadjusted risk difference of 0.055 and p = 0.007.

The primary comparison is described as a complete case analysis. The registry does not report an adjusted analysis, multiplicity strategy, missing-data sensitivity analysis, or original sample-size justification. The posted results should be read with those reporting limitations in mind.