Concurrent Alcohol and Smoking Treatment: Effects on Alcohol Relapse Risk: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Concurrent Alcohol and Smoking Treatment: Effects on Alcohol Relapse Risk (NCT00861146), a randomized phase 2 study. The primary outcome is Smoking Abstinence.

2. Clinical Question

The primary comparison concerns smoking abstinence, not whether either treatment strategy changes alcohol use or other health outcomes. Abstinence was defined as 7-day point prevalence smoking abstinence verified by breath carbon monoxide; missing values were coded as smoking. In the concurrent group, 20 of 105 participants met the endpoint, compared with 1 of 46 in the deferred group. The registry’s posted comparison expresses the deferred group relative to the concurrent group, so its negative risk difference points toward fewer observed abstinent participants in the deferred group.

The question is clinically relevant to the timing of smoking cessation within intensive alcohol treatment, but the registry outcome measures only the stated smoking endpoint at the stated time. The record does not establish the effects of other treatment schedules, longer-term abstinence, or outcomes beyond those posted. Specific eligibility criteria, the full treatment protocol, and participant-level characteristics are not reported in the registry record.

3. Trial Design

The registry identifies this as a phase 2, randomized, parallel-group trial with no masking. The study was conducted by Yale University and is listed as completed. Its recorded start was 2009-04 and its primary completion was 2013-03. Total enrollment was 151.

Participants were assigned to concurrent or deferred smoking cessation. The concurrent strategy delivered smoking cessation during intensive alcohol treatment; the deferred strategy delivered smoking cessation 12 weeks after intensive alcohol treatment. Behavioral counseling plus contingency management is listed as the intervention. The record does not detail the counseling content, the contingency schedule, the intensity or duration of alcohol treatment, or how treatment delivery and adherence were assessed.

The primary outcome was the number of participants meeting the smoking-abstinence definition at 12 weeks. The concurrent group had 105 participants and the deferred group had 46. The secondary outcome listed in the record was proportion of days heavy drinking during follow-up weeks 9-12. The numbers contributing to that posted analysis were 85 and 38, respectively; the reasons those numbers differ from the full arm counts are not reported in the registry record.

Random assignment helps structure a comparison between the assigned strategies, but the imbalance in group sizes and the absence of masking are features to keep in view when interpreting the posted results. The allocation procedure, reasons for the group-size imbalance, details of sequence generation, and analysis-population definitions are not reported in the registry record. The record also does not describe whether participants or outcome assessors were masked; it lists masking as none.

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

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 Smoking Abstinence, measured over 12 weeks.

The primary endpoint is smoking abstinence at 12 weeks, expressed as a number of participants. It uses 7-day point prevalence: whether a participant met the record’s definition of not smoking over the specified recent period. Breath carbon monoxide verification is part of that definition. Missing values were coded as smoking, so missing endpoint information does not count as abstinence in the posted outcome.

This endpoint gives a concrete, group-level count at a specified follow-up time. It captures a short window of smoking status rather than continuous abstinence over the entire study or long-term cessation. The registry does not report a longer-term smoking endpoint in the primary outcome description. Nor does this endpoint itself measure alcohol relapse, despite the trial title and the stated interest in processes reflecting risk of alcohol relapse.

The posted counts are 20 of 105 in the concurrent group and 1 of 46 in the deferred group. Those counts describe observed endpoint classifications under the registry’s definition; they do not reveal whether participants smoked on other days, whether abstinence persisted after the 12-week assessment, or why any individual was missing. The record does not report additional endpoint-validation details beyond breath carbon monoxide verification and the missing-as-smoking rule.

7. Results Posted in the Registry

• 2 Deferred Smoking Cessation: 2.2% (1/46) versus 19.0% (20/105) on control; risk difference -16.9 percentage points (95% CI -25.5 to -8.3), risk ratio 0.11 (0.02–0.83); unadjusted two-proportion z-test p = 0.006.

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.

Proportion of Days Heavy Drinking

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • 2 Deferred Smoking Cessation: mean 0.01 versus 0.03 on control; difference -0.02 (95% CI -0.05 to 0.01), standardized effect d = -0.21; z-test p = 0.144.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2 Deferred Smoking Cessation and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: proportion of days heavy drinking during follow-up weeks 9-12. Its posted summary and comparison do not show a clearly established group difference under the reported sponsor analysis or the unadjusted recalculation. This is a different outcome from smoking abstinence, measured over a different follow-up window and analyzed using a different approach. The results therefore complement the primary endpoint rather than directly replicate it.

The secondary pattern does not establish that smoking-treatment timing had no association with heavy drinking. The interval from the unadjusted recalculation includes zero, and the sponsor analysis reports p > .15; these findings mean that the posted analysis does not distinguish a group difference clearly, not that the groups have been shown equivalent. No equivalence margin or equivalence analysis is reported in the registry record.

Secondary outcomes generally carry less confirmatory weight when many outcomes or analyses may be examined, particularly if no prespecified hierarchy or multiplicity adjustment is reported. The registry lists three outcome measures and three analyses overall, but it does not report a multiplicity-control plan, the full set of outcome definitions, or which analyses were designated confirmatory. Without those details, an unadjusted secondary result should be interpreted as exploratory or supportive rather than as independent proof of a treatment effect. The record does not report other secondary endpoint results beyond the heavy-drinking outcome, so no broader pattern across additional posted secondary endpoints can be assessed.

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

• Proportion of Days Heavy Drinking

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results include a binary primary outcome and a continuous secondary outcome. The primary outcome records whether a participant met the smoking-abstinence definition. The secondary outcome is a mean proportion of days heavy drinking during follow-up weeks 9-12. General statistical explanations below clarify how the reported comparisons work; they do not add analyses beyond those recorded.

How does the primary comparison work?

For a binary endpoint, each participant is classified into one of two outcome categories for the analysis: meeting or not meeting the recorded abstinence definition. The registry reports 20 of 105 participants meeting the endpoint in the concurrent group and 1 of 46 in the deferred group. A risk difference compares the two groups’ observed proportions by subtraction. The posted estimate is defined for deferred relative to concurrent, so a negative value indicates a smaller observed proportion in the deferred group. This is a group-level contrast, not a measure of how every individual would respond under either strategy.

The unadjusted recalculation reports a risk difference of -0.169 and a confidence interval from -0.255 to -0.083. It also reports a p-value of 0.006. In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it quantify the probability that the result is due to chance. The record’s sponsor-reported test is chi-squared, with p < .01. A chi-squared test assesses whether the observed outcome counts differ across groups, subject to its statistical assumptions.

Why use a confidence interval?

In general, a confidence interval describes the range of effect values reasonably compatible with the data and the interval procedure. Its width reflects precision: wider intervals allow a broader range of effect sizes, while narrower intervals constrain that range more. For the primary outcome, the posted interval is entirely negative in the deferred-versus-concurrent direction. This supports a difference in the direction of fewer observed abstinent participants in the deferred group under the stated unadjusted comparison. It does not show that the exact estimate is certain, establish a mechanism, or settle clinical importance.

How should the secondary analysis be read?

The secondary endpoint is continuous, so the recalculation compares group means rather than event counts. The registry reports mean values and standard deviations for each group and a mean difference of -0.02 for deferred relative to concurrent. The confidence interval ranges from -0.047 to 0.007, and the unadjusted p-value is 0.144. Because the interval includes zero, the posted data are compatible with no difference as well as with values on either side of zero. This is not proof that the groups are identical. The sponsor’s mixed model regression analysis reports F = 2.04 and p > .15. That model-based analysis and the unadjusted summary-statistic recalculation are different methods, so their numerical outputs need not match exactly.

General statistical context: when data are more variable, a group mean is less precisely estimated unless there is enough information to offset that variability. For binary outcomes, the amount of information depends on the outcome counts and the group sizes. These general principles help explain why estimates and intervals should be read together; they do not justify inferring unreported design choices or participant-level patterns.

What does “unadjusted” mean?

The recalculations use the posted group summaries without adjusting for other variables. An adjusted model can account for measured covariates or repeated observations when its specification and data are available, but the registry record does not report covariate adjustment for the primary chi-squared analysis. The secondary sponsor analysis is described as mixed model regression analyses; further model details are not reported in the registry record. The unadjusted calculations and sponsor analyses should therefore be understood according to their stated methods rather than treated as interchangeable.

General statistical context: adjustment may change an estimate or its precision, especially if the adjusted variables are associated with the outcome. Whether adjustment is appropriate and how it should be performed depend on the prespecified analysis plan and available data. Those details are not reported in the registry record, so no additional adjusted result can be inferred. The recalculations are not a replacement for a sponsor analysis when the analyses differ; in this record, the discrepancy indicator is false.

Why does the outcome definition matter?

The primary endpoint counts missing observations as smoking. This rule determines how missing values contribute to the reported endpoint and makes the classification conservative with respect to counting abstinence. It does not remove uncertainty about how many values were missing, why they were missing, or whether missingness differed between groups. Those quantities are not reported in the registry record. The secondary outcome has different group counts from the full enrollment counts, but the reasons for the difference are not reported. These limitations matter because the reported summaries alone cannot show how missing or unavailable observations might affect a result.

11. Confidence Intervals and Precision

The primary risk-difference confidence interval runs from -0.255 to -0.083 for deferred relative to concurrent. Its endpoints are both negative, so the range of values supported by this interval is on the side corresponding to a lower observed abstinence proportion in the deferred group. The interval is not a guarantee that the true effect lies within those bounds, and it does not eliminate uncertainty about the estimate’s magnitude. It gives more information about plausible effect sizes than the p-value alone.

The secondary mean-difference confidence interval runs from -0.047 to 0.007. It crosses zero, so the data are compatible with no mean difference under this unadjusted calculation, as well as with differences in either direction. The interval’s placement should be considered alongside the reported means, standard deviations, group sizes, and the sponsor’s model-based result. It does not establish equivalence, since no equivalence margin or equivalence analysis is reported in the registry record.

Precision is limited by the amount of information available for each outcome. The primary endpoint counts are based on group sizes of 105 and 46; the secondary analysis includes 85 and 38. The registry does not report reasons for the secondary analysis counts or the number of missing primary assessments. Without those details, it is not possible to assess the impact of missing observations beyond the stated primary rule.

Confidence intervals describe statistical uncertainty under the method used; they do not encompass all sources of uncertainty, such as limitations in design, measurement, or generalizability. The registry record does not report the full analysis plan, model details for the secondary analysis, or the original rationale for the unequal group sizes. These omissions limit how far precision can be assessed from the posted summaries alone.

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 illustrations based on the observed effect, not the trial’s original design. For this binary outcome, the figures are participants per arm, rather than a total across both arms or a number of events. The stated 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 at the stated fraction of the observed effect. The trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the chosen effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding illustration for a 90% chance. These are prospective planning concepts, not probabilities that this completed trial found a result, and not measures of the trial’s observed power.

The displayed scenarios consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects require more participants per arm to reach the same target power under these assumptions. For the primary endpoint, the planning figures range from 52 to 278 participants per arm for 80% power and from 68 to 371 participants per arm for 90% power across those effect scenarios. The illustrations are distinct from the enrolled arm sizes of 105 and 46. They should not be used to infer that the original trial was designed around the observed result or that the trial was adequately powered for any particular effect.

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 = 0.190; treatment proportion p₁ = 0.022; average p̄ = 0.106.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4355 = 0.8536.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4189 = 0.3525.
4. n = (0.8536 + 0.3525)² / (-0.1687)² = 51.1, rounded up to 52 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 <- 0.19047619047619                          # control proportion
p1 <- 0.0217391304347826                          # 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(861146)
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 = 52 (80% power), 68 (90% power)
 75% of observed effect: n per arm = 108 (80% power), 144 (90% power)
 50% of observed effect: n per arm = 278 (80% power), 371 (90% power)
power.prop.test: 51.1 
Simulated power at n = 52 per arm: 0.854 (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. Analyses Reported by the Sponsor

For the primary endpoint, the registry reports the sponsor’s chi-squared analysis with p < .01. The unadjusted recalculation from the posted counts gives p = 0.006 and a risk-difference interval that is entirely negative for deferred relative to concurrent. Those results are consistent in their broad statistical reading: both indicate a difference in the observed abstinence counts between the groups, in the direction of fewer abstinent participants in the deferred group. The discrepancy indicator is false, so no conflict requiring precedence of one result over the other is flagged.

The registry does not report an effect estimate or confidence interval for the sponsor’s chi-squared analysis, so the recalculated risk difference and interval provide a different kind of information from its reported p-value. The p-values should not be treated as identical quantities; they arise from the stated analyses and may be reported with different precision.

For the secondary endpoint, the sponsor reports mixed model regression analyses with F = 2.04 and p > .15. The unadjusted recalculation reports p = 0.144 and a confidence interval that includes zero. These results are broadly aligned in not indicating a clear statistical distinction, but the methods are not the same. Details needed to reproduce or fully interpret the mixed model, including its specification, are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary smoking-abstinence outcome and a secondary proportion-of-days-heavy-drinking outcome. It also records three outcome measures and three analyses overall. A prespecified hierarchy among outcomes, a multiplicity adjustment, and the handling of multiple comparisons are not reported in the registry record. When several outcomes or analyses are considered, the chance of at least one apparently unusual result can increase. General statistical practice may address this through prespecification or adjustment, but the record does not establish whether such procedures were used.

The primary endpoint description states that missing values were coded as smoking. This defines how missing primary endpoint values contribute to the abstinence count; it does not disclose how many values were missing or whether missingness differed between groups. The number of missing primary assessments and reasons for missingness are not reported in the registry record. The secondary analysis includes 85 participants in the concurrent group and 38 in the deferred group, compared with full arm sizes of 105 and 46. Reasons for those analysis counts and the treatment of missing secondary measurements are not reported.

The registry does not identify an analysis population such as intention-to-treat, per-protocol, or another defined set. It also does not report whether all randomized participants were included in the primary analysis, how protocol deviations were handled, or whether sensitivity analyses were conducted. These omissions make it difficult to assess the consequences of missing data and exclusions beyond the primary endpoint’s stated coding rule.

The record gives the sponsor’s primary chi-squared test and secondary mixed model result, but it does not report a complete statistical analysis plan or the details of model specification. These missing details limit assessment of prespecification, multiplicity, and analytic choices; they should not be filled in by assumption.

16. Safety Results

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

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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalization psychiatric (2.2%), hospitalization stroke (2.2%), hospitalization gastrointestinal (2.2%), hospitalization alcohol (1.0%).

The registry reports serious adverse events in 4 of 105 participants in the concurrent group and 2 of 46 in the deferred group. It also reports other adverse events in 60 of 105 and 12 of 46, respectively. These are counts in the registry’s adverse-event fields; the record does not provide enough detail to interpret event severity beyond the serious-event classification or to determine relatedness to the interventions.

The listed serious-event terms include hospitalization psychiatric, hospitalization stroke, and hospitalization gastrointestinal, each shown as 2.2%, and hospitalization alcohol, shown as 1.0%. The registry record does not provide an arm-specific breakdown for those listed terms in the information reported, so they cannot be attributed to a particular group from these figures alone. Deaths are not reported in the registry record.

Adverse-event counts should be read as descriptive safety information, not as a randomized comparison establishing that one strategy caused more or fewer events. The record does not report event-level timing, participant-level overlap, definitions for the other adverse-event category, or an inferential comparison of safety outcomes. The group sizes also differ, so the counts alone are not a like-for-like measure of risk.

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

The posted primary result shows that more participants in the concurrent group met the trial’s 12-week smoking-abstinence definition than in the deferred group. The unadjusted risk difference and confidence interval favor the concurrent group in the observed comparison, and the sponsor’s chi-squared analysis reports p < .01. This describes the trial’s posted data under its endpoint definition; it is not a recommendation about treatment choice.

The result does not establish that the same difference would occur in other settings or among people who differ from those enrolled. The record does not report detailed eligibility criteria, participant characteristics, treatment adherence, or a full description of intervention delivery. It also does not report longer-term smoking abstinence. The endpoint concerns a seven-day prevalence measure at 12 weeks, with missing values coded as smoking, rather than uninterrupted abstinence across the full follow-up period.

The primary result does not demonstrate an effect on alcohol relapse. Although the trial’s stated interest includes processes reflecting risk of alcohol relapse and a secondary heavy-drinking measure is posted, that measure is not the same as relapse itself. Its analysis does not clearly distinguish the groups in the reported comparison. The record does not report a direct primary measure of alcohol relapse in the posted outcomes.

Statistical significance does not by itself establish clinical importance, persistence, or mechanism. The confidence interval conveys uncertainty about the size of the primary contrast, while the missing-data, analysis-population, and design details limit further interpretation. Conversely, the secondary result’s lack of a clear statistical distinction does not demonstrate that there is no difference. The posted results answer a specific comparison at specific follow-up times and leave broader questions unresolved.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two timings of smoking cessation within intensive alcohol treatment and reports a binary smoking-abstinence outcome at a defined follow-up. The concurrent and deferred groups differ in observed abstinence counts, and the posted primary interval and sponsor test both indicate a group contrast in the same direction. The result illustrates why reporting an effect estimate and confidence interval adds information beyond a significance test alone.

It also illustrates the importance of keeping endpoints distinct. Smoking abstinence is the primary outcome, while proportion of days heavy drinking is a secondary measure over follow-up weeks 9-12. The two outcomes address different questions, and a primary result should not be taken as evidence for a secondary outcome or for alcohol relapse. Different analysis methods and different numbers contributing to each endpoint further matter when comparing the results.

The record also highlights uncertainty that cannot be resolved from summary statistics. It gives a rule for missing primary values but does not report how many values were missing, and it does not explain why the secondary analysis counts are smaller than the full arm counts. It does not report the original sample-size rationale, multiplicity procedures, or analysis-population definitions. These are not minor details when assessing precision and the strength of claims.

Finally, planning illustrations based on observed effects can help readers understand how required enrollment changes with the effect targeted, but they cannot reconstruct the trial’s original design or establish observed power. Keeping that distinction clear prevents a post hoc planning exercise from being mistaken for evidence about what the study was designed to detect.

19. 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.

The registry record provides limited detail for evaluating who the results apply to. Specific eligibility criteria, participant characteristics, and the setting of intensive alcohol treatment are not reported in the registry record. The group sizes are unequal, and the reason for that imbalance is not reported. Although randomization is listed, the sequence-generation and allocation-concealment procedures are not described.

Masking is listed as none. The record does not specify whether outcome assessment was otherwise blinded or how breath carbon monoxide verification was conducted. The primary endpoint has a stated missing-as-smoking rule, but the number and reasons for missing observations are not reported. The secondary analysis includes fewer participants than the full arm counts, and the reasons are not reported. Analysis populations, protocol deviations, and sensitivity analyses are also not described.

The intervention is listed as behavioral counseling plus contingency management, but details on its content, delivery, adherence, and fidelity are not reported. The deferred arm’s timing is described relative to intensive alcohol treatment, but further details of the treatment sequence are not available. The record does not provide longer-term smoking outcomes, and its secondary heavy-drinking measure is not a direct report of alcohol relapse.

The registry does not report the trial’s original sample-size justification, full statistical analysis plan, multiplicity procedures, or detailed model specification for the secondary analysis. The sponsor’s primary analysis reports a chi-squared p-value but not an effect estimate or interval. These limits constrain assessment of prespecification, robustness, and clinical importance using the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Concurrent Alcohol and Smoking Treatment: Effects on Alcohol Relapse Risk — NCT00861146.
• Registry record last updated 2020-04-03; status last verified 2020-04.
• Results first posted 2014-04-07.
• 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.

23. Record Summary

NCT00861146 is a completed phase 2 randomized parallel-group trial sponsored by Yale University. The record lists no masking and enrollment of 151 participants. It compares smoking cessation delivered concurrently with intensive alcohol treatment against smoking cessation deferred until 12 weeks after intensive alcohol treatment.

The primary outcome is 12-week smoking abstinence, defined by 7-day point prevalence verified by breath carbon monoxide, with missing values coded as smoking. The posted counts are 20 of 105 in the concurrent group and 1 of 46 in the deferred group. The sponsor reports a chi-squared test with p < .01; the unadjusted recalculation reports p = 0.006 and a negative risk difference for deferred relative to concurrent.

The listed secondary outcome is proportion of days heavy drinking during follow-up weeks 9-12. Its sponsor analysis reports F = 2.04 and p > .15. The record does not report the original sample-size rationale, multiplicity approach, or analysis-population definitions.