Cognitive Training for Nicotine Dependence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cognitive Training for Nicotine Dependence (NCT01252966), a randomized na study. The primary outcome is Point-prevalence Abstinence at End of Treatment.

2. Clinical Question

The trial record describes a randomized comparison of two computerized training programs, not a comparison of nicotine patch therapy or counseling against no treatment. Those cessation supports were part of both arms. The contrast of interest is therefore the additional contribution associated with assignment to cognitive training rather than control training within this shared treatment setting.

Abstinence was assessed at the end of treatment, identified as Week 12. The definition required no self-reported smoking, even a puff, for at least 7 days and in-person verification using carbon monoxide breath levels below 8ppm. Participants who withdrew or were lost to follow-up were counted as smokers for the primary outcome. These operational choices are important to understanding what the primary comparison represents.

The registry record lists point-prevalence abstinence at 6-month follow-up and cognitive performance measures as secondary outcomes. It does not report further detail about who was eligible, the intended mechanism of cognitive training, or the specific hypothesis for each cognitive measure. The clinical question is consequently interpreted from the registered interventions and outcome definitions rather than from unreported protocol details.

3. Trial Design

This was a randomized, parallel-group behavioral trial with single masking. The registry record identifies the sponsor as the University of Pennsylvania, gives enrollment as 213, and lists the trial status as completed. The recorded start was 2011-03 and primary completion was 2015-09. The phase is recorded as NA.

Participants were assigned to cognitive training or control training. Both groups received 8 weeks of standard nicotine patch therapy and smoking cessation counseling. The cognitive-training arm received computerized cognitive training in addition to those supports; the control arm received computerized control training alongside them. This common background treatment helps define the trial contrast: the groups differed in the assigned training program, while the registry description says the cessation supports were shared.

The primary outcome was measured at the end of treatment, specified as Week 12. The registry also lists a 6-month abstinence outcome and cognitive performance in working memory, response inhibition, and attention. The posted results include working memory, response inhibition, and 6-month abstinence; a result for attention is not reported in the registry record. The record lists five outcome measures and four analyses.

Although the design is described as single-masked, which party or parties were masked is not reported in the registry record. The randomization sequence, allocation-concealment procedures, recruitment sites, eligibility criteria, and protocol deviations are also not reported in the registry record. The original sample-size justification, planned analysis populations, and detailed statistical plan are not reported in the registry record. Those gaps limit how fully the design can be reconstructed from the registry entry alone.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Five hundred and fifty-seven participants provided consent and 213 were randomized. Reasons for exclusion from randomization included no home computer or internet access and failure to meet final eligibility criteria at the Intake Visit.

Overall Study

Reasons for not completing this period:

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 Point-prevalence Abstinence at End of Treatment, measured over End of treatment (Week 12).

The primary endpoint was 7-day point-prevalence abstinence at the end of treatment, specified as Week 12. It measures whether a participant met the trial’s abstinence definition at that assessment; it is not a measure of continuous abstinence throughout the full treatment period. The outcome was recorded as the percentage of participants meeting the definition.

The registry description says daily smoking from the Target Quit Date through the end of treatment was assessed with a validated timeline follow-back measure. For the primary outcome, a participant had to report no smoking, even a puff, for at least 7 days. Abstinence also required in-person verification by carbon monoxide breath levels below 8ppm. Participants who withdrew or were lost to follow-up were counted as smokers.

Point-prevalence abstinence is used in smoking-cessation trials to capture abstinence over a defined recent interval at a specified assessment. That makes the endpoint interpretable as a snapshot anchored to the end of treatment, rather than as proof that abstinence persisted continuously. The registry record states that its definition followed guidelines for smoking cessation trials. It does not report further detail about the validation procedure, the handling of unsuccessful verification beyond the stated definition, or the exact assessment schedule within the treatment period.

7. Results Posted in the Registry

• Cognitive Training: 38.0% (41/108) versus 42.9% (45/105) on control; risk difference -4.9 percentage points (95% CI -18.1 to 8.3), risk ratio 0.89 (0.64–1.23); unadjusted two-proportion z-test p = 0.467.

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.

Point-prevalence Abstinence at 6-month Follow-up

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cognitive Training: 14.8% (16/108) versus 24.8% (26/105) on control; risk difference -9.9 percentage points (95% CI -20.6 to 0.7), risk ratio 0.60 (0.34–1.05); unadjusted two-proportion z-test p = 0.068.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cognitive Training and the control. The interval gives the range of effects that remain compatible with the data.

Cognitive Performance (Working Memory)

• 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:
  • Cognitive Training: mean 0.22 versus 0.03 on control; difference 0.19 (95% CI -0.15 to 0.53), standardized effect d = 0.17; z-test p = 0.278.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cognitive Training and the control. The interval gives the range of effects that remain compatible with the data.

Cognitive Performance (Response Inhibition)

• 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:
  • Cognitive Training: mean -0.84 versus -0.49 on control; difference -0.35 (95% CI -1.09 to 0.39), standardized effect d = -0.14; z-test p = 0.357.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cognitive Training and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results cover abstinence at 6-month follow-up and cognitive performance in working memory, response inhibition, and attention. The posted numerical results include the first three; an attention result is not reported in the registry record. Across the reported secondary comparisons, the recalculated intervals include the corresponding no-difference value. The pattern does not supply a clearly precise secondary contrast that independently resolves the uncertainty in the primary abstinence comparison.

The secondary outcomes address related but distinct questions. Follow-up abstinence extends the smoking outcome beyond the end-of-treatment assessment, while the cognitive measures assess performance on specific tasks. They can add context to the primary result, but they are not substitutes for it. In particular, a cognitive-performance measure does not by itself establish a change in smoking abstinence, and a later abstinence assessment does not alter the definition of the primary endpoint.

Unadjusted secondary findings generally carry less confirmatory weight when several outcomes are examined. Each additional analysis creates more opportunities for an apparently unusual result to occur by chance. The registry record lists multiple outcome measures and analyses, but does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the secondary outcomes. Without that information, secondary p-values should be regarded as exploratory rather than as independent confirmation of the primary comparison.

The registry record also does not report the complete results for every listed secondary outcome in the information available: attention is listed as an outcome, but its result is not reported in the registry record. Missing secondary results make it harder to assess the full pattern of analyses and the possibility of selective reporting. The secondary findings should therefore be interpreted alongside the primary result and with attention to the limits of the registered record, rather than treated as a collection of separate definitive tests.

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

• Point-prevalence Abstinence at 6-month Follow-up
• Cognitive Performance (Working Memory)
• Cognitive Performance (Response Inhibition)
• Cognitive Performance (Attention)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

For a binary endpoint such as abstinence, a risk is the proportion of participants in a group who meet the outcome definition. A risk difference subtracts the comparator-group proportion from the intervention-group proportion. The recalculated estimate is -0.049 for cognitive training relative to control training. A value below zero means the observed proportion was lower in the cognitive-training group under this direction of comparison. The estimate is an absolute contrast on the risk scale, rather than a ratio of the groups’ risks.

General statistical explanation: an absolute difference and a relative measure answer different questions. A risk difference describes the distance between group proportions; an odds ratio compares the odds of the outcome. The numerical values are not expected to be the same because the scales differ. Neither measure alone describes the uncertainty; that is why an interval estimate is also useful.

What does logistic regression add?

The registry reports a logistic-regression analysis for the primary outcome, expressed as an odds ratio. Logistic regression models the log odds of a binary outcome. The registry gives an odds ratio of 0.69, a 95% confidence interval from 0.42 to 1.13, and p = 0.14. The record does not report which predictors or covariates were included, so the degree of adjustment cannot be determined. The recalculation instead uses the posted group summaries to form an unadjusted risk difference and an unadjusted p-value of 0.467.

General statistical explanation: regression can account for measured variables included in a model, whereas a simple summary-based comparison does not. A model-based estimate and an unadjusted estimate can therefore differ in both scale and value. That difference is not, by itself, evidence of an error. Interpretation depends on the specified model, outcome coding, and comparison direction, details that are not fully reported for the registry analysis.

How should the p-values be read?

A p-value is calculated relative to a statistical model and a null hypothesis. It describes how unusual data at least as discrepant as those observed would be if the model’s null hypothesis held. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of an effect. The reported regression p-value and the recalculated unadjusted p-value arise from different analyses and should be read with their respective estimates.

General statistical explanation: p-values can change with the outcome scale, model, covariate adjustment, and analysis assumptions. They do not summarize all uncertainty in the data. A p-value above a conventional threshold does not establish equivalence; an equivalence claim ordinarily requires a prespecified margin and an analysis designed to assess that margin. Such a margin or equivalence analysis is not reported in the registry record.

What do the continuous outcomes measure?

The cognitive performance results are reported as mean changes from baseline to Week 12, with standard deviations. For working memory, the measure is change in maximum recall span. For response inhibition, it is change in the number of commission errors. The recalculated comparisons use mean differences between arms. A mean difference expresses the separation in average change on the measure’s own scale; it is not a percentage or an odds ratio.

General statistical explanation: a standard deviation describes variation among individual measurements around a group mean. It is different from a confidence interval, which describes uncertainty in an estimated quantity. A mean difference can be interpreted in the original measurement units, but its practical importance depends on what changes in that measure mean and whether the measure is reliable and relevant. Those interpretation details are not reported in the registry record.

Why can a confidence interval be more informative than a single estimate?

An estimate gives one central value for the observed comparison, while an interval expresses a range of values compatible with the data and the method used. For the primary recalculation, the interval extends from -0.181 to 0.083. It contains zero, the value corresponding to no risk difference. Thus, the estimate does not narrowly pin down the direction or magnitude of the contrast.

General statistical explanation: an interval is not a guarantee that the true effect lies within its endpoints, and its meaning depends on the method and assumptions used to construct it. The registry gives a 95% confidence level for the sponsor’s odds-ratio interval. A confidence level for the recalculated intervals is not reported in the registry record, so the sponsor’s stated confidence level should not be assigned to those recalculated intervals.

Why does over-dispersion matter in general?

General statistical explanation: over-dispersion occurs when the observed variability is greater than a model assumes. If a model underestimates variability, its standard errors may be too small and its intervals too narrow, making the evidence appear more precise than it is. The posted primary endpoint is binary, and the cognitive outcomes are reported as means and standard deviations. The registry does not report an over-dispersion assessment, so no conclusion about over-dispersion in this trial can be drawn from the record.

The record does not report the full analysis plan, model diagnostics, covariate specification, or procedures for handling multiple testing. The recalculated comparisons are simple, unadjusted comparisons from the posted arm summaries; they do not replace the sponsor’s own analysis. This distinction matters because the recalculation answers a narrower question than a fully specified trial analysis could answer.

11. Confidence Intervals and Precision

The recalculated primary risk difference is -0.049, with an interval from -0.181 to 0.083. Because the interval includes zero, the data are compatible with no risk difference as well as with contrasts in either direction under the recalculation method. The interval’s breadth indicates that the estimate is not highly precise. Its endpoints should be read as uncertainty bounds for this estimate, not as observed group outcomes.

The sponsor’s logistic-regression estimate is on the odds-ratio scale: 0.69, with a 95% confidence interval from 0.42 to 1.13. That interval includes 1, the no-association value for an odds ratio. The registry does not report covariates used in the model, so the role of adjustment in the sponsor estimate cannot be assessed. The recalculated risk-difference interval and the sponsor odds-ratio interval describe different scales and should not be compared endpoint for endpoint.

For the 6-month abstinence recalculation, the risk difference is -0.100, with an interval from -0.206 to 0.007. For working memory, the mean difference is 0.19, with an interval from -0.153 to 0.533. For response inhibition, the mean difference is -0.35, with an interval from -1.094 to 0.394. These intervals also include their respective no-difference values. A result interval for attention is not reported in the registry record.

General statistical explanation: precision depends on the amount of information and the variability of the outcome, among other factors. A confidence interval is not a measure of whether an effect matters clinically. It indicates the uncertainty associated with an estimate under a specified method. The registry does not state the confidence level used for the recalculated intervals; only the sponsor’s primary odds-ratio interval is explicitly labeled as 95%.

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 specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm under which a study would have an 80% chance of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities under assumptions, not probabilities that the result is true or that a particular study will be positive.

Rows planning for 100%, 75%, or 50% of the observed effect represent progressively smaller effects to detect. Smaller effects generally require more participants to distinguish them from random variation under otherwise similar assumptions. The resulting sample sizes are illustrations based on the observed effect, not the trial’s original design calculation. They do not show that the completed trial had a particular probability of success. This is not observed power.

Because the planning assumptions use equal allocation and a normal approximation, the figures should be understood as scenario-based planning estimates rather than a reconstruction of the trial protocol. The registry record does not report the original target effect, attrition allowance, or other design considerations used when the trial was planned.

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 = 0.429; treatment proportion p₁ = 0.380; average p̄ = 0.404.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6940 = 1.3602.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6931 = 0.5833.
4. n = (1.3602 + 0.5833)² / (-0.0489)² = 1,576.9, rounded up to 1,577 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 <- 0.428571428571429                          # control proportion
p1 <- 0.37962962962963                          # 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(1252966)
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 = 1,577 (80% power), 2,111 (90% power)
 75% of observed effect: n per arm = 2,818 (80% power), 3,772 (90% power)
 50% of observed effect: n per arm = 6,369 (80% power), 8,526 (90% power)
power.prop.test: 1576.9 
Simulated power at n = 1,577 per arm: 0.799 (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

The sponsor’s primary analysis is a logistic regression reported as an odds ratio of 0.69, with a 95% confidence interval from 0.42 to 1.13 and p = 0.14. The recalculation is an unadjusted comparison of the posted group summaries, expressed as a risk difference of -0.049, with an unadjusted p-value of 0.467. These are not duplicate calculations of the same statistic: one is an odds ratio from regression, while the other is an absolute difference in proportions calculated without regression adjustment.

Different scales and modeling choices can produce different numerical estimates and p-values. The registry record does not specify the regression covariates or other model details, so it is not possible to reproduce the sponsor analysis from the record. Both reported analyses have intervals that include their respective no-difference values, but that does not establish equivalence or prove the absence of an effect.

The recalculation is useful as a transparent, simple comparison of the posted summaries. It is not a replacement for the sponsor’s analysis, which takes precedence as the registry’s reported analysis. The registry record does not report a discrepancy between the two analyses. The two p-values should therefore be described with their methods and interpreted separately rather than treated as competing versions of a single identical test.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes, including the primary end-of-treatment abstinence measure, 6-month abstinence, and cognitive performance measures. The record lists five outcome measures and four analyses. It does not report whether the analysis plan controlled the overall false-positive risk across outcomes, whether one outcome was prioritized over others beyond the designation of a primary outcome, or whether any hierarchical testing strategy was used. A multiplicity adjustment is not reported in the registry record.

General statistical explanation: when several hypotheses are tested, the chance of at least one small p-value arising by chance can increase. Adjustment procedures or a prespecified testing hierarchy can address that issue, but they may change how results are interpreted. Since the registry does not report a multiplicity procedure, the secondary p-values should not be treated as if they were automatically adjusted or as a set of independent confirmatory findings.

The primary endpoint definition explicitly classifies participants who withdrew or were lost to follow-up as smokers. That is a stated handling rule for the primary outcome. The registry record does not report the counts of withdrawals or losses to follow-up, the timing of missing assessments, or sensitivity analyses under other assumptions. It also does not report how missing values were handled for the secondary abstinence or cognitive outcomes.

The analysis populations, including whether analyses followed intention-to-treat principles for every outcome, are not reported in the registry record. The registry does not give a participant flow by arm or explain exclusions from individual analyses. The cognitive outcomes include fewer participants than the primary arm totals, but reasons for the analysis sample sizes are not reported in the registry record. These omissions limit assessment of missing-data bias and whether the analyzed groups remained comparable after randomization.

The regression covariates, model diagnostics, and detailed prespecified statistical methods are also not reported. Consequently, the registry permits a description of the reported analysis and a simple unadjusted recalculation, but not a full audit of adherence to the original analysis plan.

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: surgery (gastric bypass) (1.9%), breast cancer (1.0%), squamous cell carcinoma (0.9%), infection (0.9%), pancreatitis (0.9%).

The registry reports serious adverse events in 6 of 108 participants in the cognitive-training group and 3 of 105 in the control-training group. Other adverse events are reported for 42 of 108 and 54 of 105 participants, respectively. These are counts of participants with events, not rates calculated over person-time. The registry record does not report deaths; death counts should not be interpreted as zero.

The listed serious adverse-event terms include Surgery (Gastric Bypass) at 1.9%, Breast Cancer at 1.0%, Squamous Cell Carcinoma at 0.9%, Infection at 0.9%, Pancreatitis at 0.9%, and Emergency Procedure at 0.9%. These terms describe events recorded in the trial; the registry information does not establish that the training assignment caused them. The record does not provide event-level timing, duration, severity grading beyond the serious-event designation, or an assessment of relatedness for each event.

Comparing these counts descriptively does not establish a safety difference. The groups differ in size, and the record does not provide a formal statistical analysis of adverse events. The available figures should be read as registry-reported counts during the trial, not as proof of causation or as a comprehensive safety profile.

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

The results describe a randomized comparison of cognitive training with control training when both groups also received nicotine patch therapy and smoking cessation counseling. At the end-of-treatment assessment, the observed abstinence percentages were 38.0% and 43.0%, respectively. The unadjusted risk-difference estimate is -0.049, and its interval from -0.181 to 0.083 includes zero. The sponsor’s logistic-regression analysis also reports an interval that includes its no-association value. Together, these results leave uncertainty about the size and direction of the difference between the training assignments.

They do not demonstrate that the two training programs are equivalent. Equivalence requires a defined margin and an analysis designed to determine whether the uncertainty falls within that margin; neither is reported in the registry record. Nor do the results prove that cognitive training has no effect. A nonsignificant p-value is not evidence of exact equality, and the available intervals allow a range of possible contrasts.

The results also do not isolate the effects of nicotine patch therapy or counseling, because both were given to both groups. They address the comparison between the assigned computerized programs in that shared setting. The primary endpoint is a defined recent abstinence status at end of treatment, with biochemical verification and a rule counting withdrawals and losses as smokers. It is not a measure of uninterrupted abstinence for the entire period.

The posted secondary findings offer additional, but incomplete, context. Results are not reported for the listed attention outcome, and the registry does not report multiplicity procedures or detailed missing-data analyses. The numerical findings should therefore be interpreted as evidence from the registered outcomes and analyses, not as a complete account of every possible outcome or as a basis for individual treatment decisions.

Overall, the trial’s posted data quantify an uncertain contrast in abstinence and cognitive outcomes. They do not by themselves establish clinical importance, explain the mechanism of any observed difference, or support conclusions about populations and settings not described in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of effect measure matters. The sponsor reports an odds ratio from logistic regression, whereas a simple recalculation from the group summaries expresses the primary comparison as an absolute risk difference. The two scales answer related but different questions, and the registry does not provide enough model detail to reproduce the sponsor estimate. Reporting both clearly, with their methods, avoids treating unlike estimates as though they were interchangeable.

The primary interval is also a useful reminder that a point estimate alone can obscure substantial uncertainty. The recalculated estimate has a direction, but its interval includes zero and extends to values on either side of no difference. A p-value alone would not communicate the range of contrasts compatible with the data. Statistical interpretation is stronger when it considers the estimate, its interval, the endpoint definition, and the analysis method together.

The trial also demonstrates the importance of separating the target comparison from shared background care. Both arms received nicotine patch therapy and counseling, so the randomized contrast concerns cognitive training versus control training on top of those supports. This distinction prevents the results from being misread as an evaluation of the shared cessation treatment.

Finally, the registry entry highlights how incomplete reporting constrains interpretation. Details about regression covariates, multiplicity, analysis populations, and missing secondary outcomes are not reported. Those details matter for assessing precision, reproducibility, and the weight given to exploratory findings. The trial is statistically instructive not because one p-value settles the question, but because it shows how design, outcome definitions, effect scales, uncertainty, and reporting completeness jointly shape what can be concluded.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the eligibility criteria or further characteristics of the enrolled population. This limits assessment of how closely the trial participants resemble other groups with tobacco use disorder or nicotine addiction. Recruitment sites and setting are also not reported in the registry record, so setting-specific context cannot be evaluated.

The meaning of single masking is not specified: the record does not identify who was masked or describe how masking was maintained. Allocation concealment and the randomization procedure are not reported. These omissions limit assessment of potential bias in assignment and outcome assessment, even though the trial is registered as randomized.

The primary analysis is reported as logistic regression, but the model covariates and diagnostics are not reported. The registry does not provide a full statistical analysis plan, an original sample-size justification, or a prespecified effect size for planning. It also does not report whether multiplicity was controlled across outcomes. These gaps mean that the posted summary cannot establish whether all modeling and testing decisions followed a prespecified plan.

Missing-data reporting is limited. Withdrawals and losses to follow-up were counted as smokers for the primary outcome, but their numbers and timing are not reported. Handling of missing secondary abstinence and cognitive measurements, reasons for differing analysis sample sizes, and sensitivity analyses are not reported in the registry record. The attention outcome is listed, but its result is not reported in the registry record.

The follow-up abstinence result and cognitive measures add breadth, but multiple secondary analyses increase the importance of prespecification and multiplicity reporting. The available record does not support a complete evaluation of those issues. Finally, the adverse-event counts are descriptive and lack reported event-level details and formal comparative analyses. These limitations do not negate the registered findings; they define the uncertainty and reporting gaps that should accompany their interpretation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Cognitive Training for Nicotine Dependence — NCT01252966.
• Registry record last updated 2017-01-16; status last verified 2017-01.
• Results first posted 2017-01-02.
• 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

NCT01252966, titled Cognitive Training for Nicotine Dependence, is recorded as a completed randomized, parallel-group, single-masked behavioral trial with enrollment of 213. Both groups received standard nicotine patch therapy and smoking cessation counseling; the randomized contrast was computerized cognitive training versus computerized control training.

The primary outcome was 7-day point-prevalence abstinence at end of treatment, specified as Week 12. The registry reports an arm-level result and a logistic-regression odds ratio of 0.69, with a 95% confidence interval from 0.42 to 1.13 and p = 0.14. An unadjusted recalculation gives a risk difference of -0.049, with an interval from -0.181 to 0.083 and p = 0.467.

Secondary results include 6-month abstinence and cognitive performance measures. An attention result, detailed missing-data analyses, multiplicity procedures, regression covariates, and the original sample-size justification are not reported in the registry record. The posted results support a description of the observed comparisons, while leaving uncertainty about their precision and the full analysis context.