Counseling and Nicotine Replacement Therapy in Helping Adult Smokers Quit Smoking: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Counseling and Nicotine Replacement Therapy in Helping Adult Smokers Quit Smoking (NCT00365508), a randomized phase 4 study. The primary outcome is 24-hour Point Prevalence Abstinence at the 6-month Follow up.

2. Clinical Question

3. Trial Design

The registry describes a randomized, unmasked trial with a factorial model and phase 4 classification. Enrollment was 642, and each listed arm included 321 participants. The registry labels the intervention arms as Arm I and Arm II: Arm I received nicotine patches and Arm II received nicotine lozenges. The brief summary describes counseling alongside nicotine replacement therapy in both comparisons.

The patch schedule used a higher dose during weeks 3-8, a medium dose during weeks 9-10, and a lower dose during weeks 11-14. The lozenge schedule specified one lozenge every 1-2 hours during weeks 3-8, with a minimum of 9 lozenges per day; one every 2-4 hours during weeks 9-11, with a minimum of 5 per day; and one every 4-8 hours during weeks 12-14, with a minimum of 3 per day.

Masking is listed as none, so participants and trial staff were not masked according to the registry classification. The record labels the model factorial, but further detail about the factors or their structure is not reported in the registry record. The record lists phase 4, while its brief purpose describes a randomized phase III trial; the reason for that difference is not reported in the registry record. The study is marked completed. Its start is listed as 2006-02 and primary completion as 2009-08.

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: 1299 individuals were screened for this trial over 4 years; 454 individuals were ineligible, 194 refused enrollment, and 651 were randomized. Nine individuals either withdrew from the study prior to treatment or were found to be ineligible after randomization and were removed from the intent-to-treat sample. The final ITT sample was 642 (321/arm).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat analysis (lost to follow-up = smoker)

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 24-hour Point Prevalence Abstinence at the 6-month Follow up, measured over 6-months.

The primary endpoint is the number of participants with 24-hour point-prevalence abstinence at the 6-month follow-up. In plain terms, it counts participants classified as abstinent over a 24-hour period at that follow-up. It is a snapshot of smoking status, not a measure of continuous abstinence across the interval since treatment began. The registry identifies the analysis population as intent to treat and specifies that participants lost to follow-up are counted as smokers.

In general, a point-prevalence endpoint is useful for describing smoking status at a defined follow-up because it applies the same short-window definition to each arm. It does not, on its own, establish how long a participant had been abstinent, whether there were periods of resumed smoking, or whether the result would persist beyond the assessment. The registry does not report additional endpoint-definition details, such as the method used to verify abstinence. The posted counts are 50 in the patch arm and 35 in the lozenge arm; the corresponding posted proportions are 0.156 and 0.109.

7. Results Posted in the Registry

• Arm II: 10.9% (35/321) versus 15.6% (50/321) on control; risk difference -4.7 percentage points (95% CI -9.9 to 0.6), risk ratio 0.70 (0.47–1.05); unadjusted two-proportion z-test p = 0.081.

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.

Rate of Compliance During the First 2 Weeks

• 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:
  • Arm II: 27.1% (87/321) versus 72.0% (231/321) on control; risk difference -44.9 percentage points (95% CI -51.8 to -37.9), risk ratio 0.38 (0.31–0.46); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Arm II than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary endpoint, compliance during the first 2 weeks. Its comparison pattern differs from the primary abstinence comparison: the posted secondary analysis favors the patch arm on the recorded compliance measure, while the primary estimate also points toward the patch arm but has substantial uncertainty. These outcomes address different aspects of the trial. Compliance is not the same as abstinence at follow-up, and a difference in one should not be treated as proof of a difference in the other.

In general, a secondary endpoint can help describe treatment use or provide context for the primary finding, but it does not replace the primary question. Compliance measures may reflect behavior during treatment, whereas an abstinence endpoint reflects smoking status at follow-up. The registry does not provide further detail on how compliance was defined, so the meaning of that measure should be kept to its posted label.

The secondary comparison is an unadjusted analysis. In general, when several outcomes or analyses are examined, the chance of finding a seemingly notable result by chance can increase. Adjusting for multiple comparisons is one way to address that issue, but no multiplicity adjustment is reported in the registry record. The secondary result should therefore carry less weight than a prespecified primary result, particularly when the analysis plan and multiplicity strategy are not reported.

The secondary finding may be considered alongside the primary outcome as descriptive context, not as independent confirmation of the primary result. The registry does not report a detailed hierarchy of outcomes or a plan for interpreting secondary analyses. The posted data consequently do not establish whether the secondary measure was intended to support a particular explanation of the primary comparison.

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

• Rate of Compliance During the First 2 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

The principal comparison concerns a binary outcome: each participant is classified according to whether the endpoint was met. The reported arm values are counts, while the comparison statistics express differences or relative contrasts between the arms. The primary comparison uses Arm I, the patch arm, as the reference and compares Arm II, the lozenge arm, against it.

What does a risk difference describe?

In general, a risk difference subtracts the event proportion in the reference group from the event proportion in the comparison group. A negative value means the event proportion is lower in the comparison group; a positive value means it is higher. Here, the posted risk difference is -0.047. The registry reports its 95% confidence interval as -0.099 to 0.006. The interval crosses zero, the value corresponding to no difference in proportions. The estimate is an absolute contrast on the proportion scale, while the arm-specific proportions describe the event level in each group.

How do relative measures differ?

In general, a risk ratio compares the event proportions by division, and an odds ratio compares the odds of the event. These relative measures use different scales from the risk difference, so their numerical values should not be read as if they were interchangeable. The registry posts a risk ratio of 0.7 and an odds ratio of 0.663 for the primary comparison. Their confidence intervals include 1, the value corresponding to no relative difference. The direction of these estimates is consistent with the lower observed proportion in the lozenge arm, but the intervals show uncertainty about the size and direction of the underlying contrast.

What does the p-value say?

In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the test assumptions held. It is not the probability that the null hypothesis is true, nor does it measure the probability that chance alone caused the result. The unadjusted re-calculation has p = 0.081. The registry separately reports a chi-squared analysis with p = .05. The record does not provide enough detail to reconstruct the registry test or explain the difference between these results.

Why can confidence intervals and p-values be useful together?

In general, a confidence interval shows a range of estimates compatible with the data and the method’s assumptions, while a p-value summarizes evidence relative to a specified null value. The interval also conveys the range of effect sizes that remain plausible under that method. A result near a conventional threshold should not be treated as a sharp boundary between meaningful and meaningless evidence. The width and location of the interval matter, as do endpoint definition, missing-data handling, and analysis choices.

What is the role of the chi-squared test?

In general, a chi-squared test assesses whether the distribution of a categorical outcome differs across groups. For a binary endpoint and two arms, it can test whether the observed proportions are compatible with equal proportions, subject to its assumptions. The registry identifies the reported method as chi-squared but does not give the test statistic, the exact implementation, or details of any adjustment. The posted re-calculation is described as unadjusted; it should not be confused with an adjusted model or with the sponsor’s own analysis.

What does intent to treat mean in this record?

In general, an intent-to-treat analysis aims to retain participants in their randomized groups for analysis, regardless of treatment adherence. The registry states that its primary analysis uses this population and classifies participants lost to follow-up as smokers. This rule makes the handling of missing outcome data explicit, but the number of missing outcomes and any additional missing-data analyses are not reported in the registry record. Because missing outcomes are assigned a specific status, the result depends partly on that convention as well as on the observed outcomes.

Why does unmasked allocation matter?

In general, a lack of masking can affect behavior, adherence, expectations, and how outcomes are assessed. The endpoint is smoking status, but the registry does not report whether assessment was blinded or how abstinence was verified. It is therefore not possible to determine from the record whether awareness of assignment influenced outcome assessment. This is a potential design consideration, not evidence that bias occurred.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.047, and its 95% confidence interval extends from -0.099 to 0.006. The interval spans zero, meaning that the posted data and calculation are compatible with no difference as well as with estimates favoring either arm. The central estimate points toward a lower abstinence proportion in the lozenge arm, but the interval does not support a precise claim about the magnitude of the contrast.

In general, a confidence interval gives a range of values that are compatible with the observed data under the statistical method and its assumptions. It does not guarantee that the true value lies in the interval, and it does not account for every source of uncertainty, such as outcome misclassification or departures from the analysis assumptions. The width of an interval reflects statistical precision: a narrower interval generally indicates more precision, while a wider interval leaves more uncertainty about the effect size.

The relative-effect intervals also cross their no-difference value. The risk-ratio interval is 0.468 to 1.048, and the odds-ratio interval is 0.417 to 1.054. These intervals reinforce that the estimate is not precise enough to exclude no relative difference using these calculations. They should be interpreted on their respective scales, not translated into one another.

The registry’s chi-squared result does not include a confidence interval, so the precision of that sponsor-reported analysis cannot be judged from its posted result alone. Confidence intervals also do not address all questions about practical importance. The registry does not report a threshold for a clinically important difference, so the practical meaning of the range cannot be anchored to such a threshold from this record.

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.

Each planning value is expressed as participants per arm, not as a total across arms or as total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect as a starting point and show planning for 100%, 75%, and 50% of that observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column means the illustrated number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were true. The 90% power column gives the corresponding planning target for a 90% chance under those assumptions. These are design probabilities, not probabilities that the trial result is correct. The displayed figures are planning illustrations, not observed power.

For the primary endpoint, the planning figures increase as the target effect becomes smaller: planning for 100% of the observed effect requires 825 participants per arm for 80% power and 1,104 participants per arm for 90% power; planning for 75% requires 1,522 and 2,037; planning for 50% requires 3,546 and 4,746. In general, smaller effects are harder to distinguish from random variation and therefore require more participants under otherwise similar assumptions.

The curve should be read as another representation of how planning requirements change with the target effect under the stated assumptions. It does not report the trial’s observed power or establish what the original investigators planned. The figures depend on the observed effect used as their reference, so they are illustrations rather than a justification of the completed study’s design.

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 = 0.156; treatment proportion p₁ = 0.109; average p̄ = 0.132.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4793 = 0.9394.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4782 = 0.4024.
4. n = (0.9394 + 0.4024)² / (-0.0467)² = 824.6, rounded up to 825 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 <- 0.155763239875389                          # control proportion
p1 <- 0.109034267912773                          # 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(365508)
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 = 825 (80% power), 1,104 (90% power)
 75% of observed effect: n per arm = 1,522 (80% power), 2,037 (90% power)
 50% of observed effect: n per arm = 3,546 (80% power), 4,746 (90% power)
power.prop.test: 824.6 
Simulated power at n = 825 per arm: 0.802 (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 registry reports the sponsor’s analysis as a chi-squared test with p = .05. It does not post an effect estimate, confidence interval, or test statistic for that analysis, so its precision and exact numerical result cannot be compared in full with the unadjusted re-calculation.

The unadjusted re-calculation reports a risk difference of -0.047, with a 95% confidence interval from -0.099 to 0.006 and p = 0.081. It is a simple calculation from the posted group summaries, not a replacement for the registry’s own analysis. The two p-values differ, and the record does not state why. Possible explanations should not be guessed: the test implementation, analysis details, or other choices are not reported in the registry record.

The discrepancy flag is false, so the record does not identify a discrepancy requiring the sponsor’s analysis to take precedence. The sponsor result and the re-calculation should nevertheless be kept distinct because they are reported through different levels of detail. The sponsor’s p-value alone does not supply an effect size or uncertainty interval. Conversely, the re-calculation does not establish that the sponsor’s method was wrong. The registry does not report enough information to adjudicate the difference, and neither result should be presented as a substitute for the missing analysis details.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and one posted secondary endpoint. It reports one analysis for the primary comparison, while the secondary endpoint has an unadjusted comparison and no sponsor-reported analysis listed. The registry record does not report a multiplicity strategy, such as an adjustment to account for examining more than one outcome, nor does it describe a hierarchy governing interpretation of the outcomes. In general, without such a plan, secondary findings are more appropriately treated as exploratory or descriptive than as stand-alone confirmatory evidence.

The primary analysis population is described as intent to treat, with lost-to-follow-up participants counted as smokers. This is a defined missing-outcome rule, but the number of participants lost to follow-up is not reported in the registry record. The record also does not report sensitivity analyses using alternative missing-data assumptions, the timing or pattern of missingness, or reasons for loss to follow-up. The effect of the specified rule on the result therefore cannot be assessed from the posted information.

The record does not report the protocol’s statistical analysis plan, the original sample-size justification, interim analyses, subgroup analyses, or whether any outcome definitions or methods changed during the study. This absence does not show that such procedures did or did not occur; it means they are not reported in the registry record. The reported chi-squared method is identified, but further details of the sponsor’s analysis are not posted. The difference between that reported p-value and the simple unadjusted re-calculation cannot be explained from the available analysis description.

These reporting gaps limit assessment of how completely the posted analyses reflect the original plan. They also make it difficult to judge the potential influence of selective reporting, unreported analytic choices, or missing outcomes. These are limits on what can be concluded from the registry record, not evidence that any particular problem occurred.

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 1% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: stroke (0.6%), seizure (0.3%), killed in car accident (0.3%), heart disease (0.3%), ulcer (0.3%).

The registry posts serious adverse event counts of 4 in the patch arm and 7 in the lozenge arm. Each arm lists 321 participants at risk. These are group-level counts; the record does not provide individual event histories or enough detail to determine whether a participant experienced more than one event. It also does not report a causal assessment linking these events to study treatment.

The listed serious-event terms include Stroke at 0.6%, Seizure at 0.3%, killed in car accident at 0.3%, Heart disease at 0.3%, ulcer at 0.3%, and appendicitis at 0.3%. The registry does not specify in this listing how the terms are distributed between arms. Other adverse events are recorded as 0 in each arm. Death counts are not reported in the registry record.

In general, adverse-event counts describe events observed and recorded during a study; they do not by themselves establish whether an intervention caused an event. The record does not report event timing, severity beyond the serious-event classification, relatedness assessments, or a comparative safety analysis. The posted counts should therefore be read descriptively, not as proof of a causal difference between the arms.

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

The posted results describe a randomized comparison of counseling with nicotine lozenges against counseling with nicotine patches. For the primary endpoint, the observed abstinence count and proportion are higher in the patch arm. The unadjusted risk-difference estimate points in that direction, but its confidence interval includes zero and its p-value is 0.081. The registry’s own analysis reports p = .05, without posting an effect estimate or interval. The record does not provide enough detail to resolve the difference between these analyses.

These findings do not establish that either treatment works or does not work. They describe the outcome recorded at the 6-month follow-up and the uncertainty around a particular comparison. The endpoint is 24-hour point-prevalence abstinence, not continuous abstinence across the study period. The registry’s rule that lost-to-follow-up participants count as smokers is also part of the result’s definition, while the number of such participants is not reported in the registry record.

In general, randomized allocation helps make group comparisons interpretable by reducing systematic differences at assignment, but it does not guarantee that every source of bias or uncertainty is absent. The trial is unmasked, and the record does not report how abstinence was verified or whether outcome assessment was blinded. Those omissions limit evaluation of the endpoint’s measurement. The registered comparison also does not provide a basis for conclusions about groups or settings not described in the record.

The primary result is therefore a comparison with a direction that favors the patch arm in the observed data, alongside uncertainty that does not exclude no difference under the posted re-calculation. It does not answer whether a different abstinence definition, longer follow-up, different counseling approach, or alternative analysis would yield the same pattern. Those questions are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate, its uncertainty, and the analysis that produced it should be considered together. The primary point estimate is not the whole result: the confidence interval crosses the no-difference value, while the registry’s reported chi-squared p-value and the unadjusted re-calculation are not identical. Because fuller sponsor-analysis details are not reported, readers cannot infer that the two procedures are equivalent or determine why their p-values differ.

It also demonstrates the value of distinguishing an absolute effect measure from relative measures. The risk difference describes the contrast in proportions on an absolute scale, while the risk ratio and odds ratio express relative contrasts. Reporting estimates with intervals makes the uncertainty more visible than a threshold-based label alone. In general, a p-value near a conventional boundary should not be treated as a categorical verdict.

The intent-to-treat rule is another statistically important feature. Counting lost-to-follow-up participants as smokers gives a clear operational definition, but the amount of missing outcome data is not reported, and alternative assumptions are not shown. Transparent reporting of the missing-data pattern and sensitivity analyses would help readers judge how dependent the comparison is on that rule.

Finally, the planning illustrations show that the required sample size depends on the target effect and desired power under stated assumptions. They are not evidence of the trial’s original design rationale or its observed power. Taken together, these features make the record useful for understanding how endpoint definition, estimation, uncertainty, analysis choices, and planning assumptions shape interpretation of a clinical comparison.

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 leaves several trial-specific details unreported. Eligibility criteria beyond the description of adult smokers, the counseling content, the nicotine replacement products’ full administration details, and how treatment use was monitored are not reported in the registry record. The arm schedules are described, but they do not provide enough information to assess all aspects of treatment delivery.

The trial is classified as unmasked. The registry does not report whether smoking status was verified by an objective method, how the 24-hour abstinence status was assessed, or whether outcome assessors were blinded. The primary endpoint is a short-window status at the 6-month follow-up, so it does not describe continuous abstinence. The number lost to follow-up is not reported, even though the analysis rule classifies those participants as smokers.

The posted primary result includes an unadjusted re-calculation and a sponsor-reported chi-squared p-value, but the sponsor analysis lacks an effect estimate and confidence interval. The reason for the difference in p-values is not reported. The registry also does not report multiplicity handling, the original sample-size rationale, interim analyses, or detailed statistical analysis plans. As a result, it is not possible to assess whether all reported analyses followed a prespecified plan.

The registry labels the design factorial, but the factors and their structure are not described. It also classifies the study as phase 4 while the brief purpose calls it phase III; the reason for this difference is not reported. These are limitations in the information available for interpreting the registered record, not proof that the study itself lacked procedures or documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Counseling and Nicotine Replacement Therapy in Helping Adult Smokers Quit Smoking — NCT00365508.
• Registry record last updated 2016-03-29; status last verified 2016-03.
• Results first posted 2013-01-30.
• 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

The completed randomized, unmasked trial compares counseling with nicotine patches against counseling with nicotine lozenges in adult smokers. The registry lists enrollment of 642 and 321 participants in each arm. Its primary endpoint is 24-hour point-prevalence abstinence at the 6-month follow-up, analyzed by intent to treat with lost-to-follow-up participants counted as smokers.

The posted primary comparison favors the patch arm in its point estimate, but the unadjusted risk-difference confidence interval includes zero. The registry also reports a chi-squared p-value of .05, while the simple re-calculation reports p = 0.081; the reason for the difference is not reported. One secondary outcome concerns compliance during the first 2 weeks. Further details about missing outcomes, analysis planning, and multiplicity are not reported in the registry record.