Smoking Cessation After Hospitalization for a Cardiopulmonary Illness: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Smoking Cessation After Hospitalization for a Cardiopulmonary Illness (NCT01791803), a randomized na study. The primary outcome is Abstinence From Smoking.

2. Clinical Question

The clinical question is about the comparative results of several cessation approaches in this hospitalized population, rather than a comparison with no contact or counseling at all: the registry describes some counseling in each group. The reported primary comparisons use hypnotherapy as the reference group, while the sponsor’s reported analyses include pairwise risk ratios for two other group pairs. The registry does not report a single stated hypothesis covering all arms, nor does it specify whether any comparison was designated as the principal treatment contrast.

The results describe abstinence at a particular follow-up point after hospitalization. They do not by themselves establish whether differences persist beyond that point, or apply to people outside the population described by the record. Further details about participant characteristics, recruitment, and the illnesses represented are not reported in the registry record.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. Its status is completed. The listed enrollment is 164. The sponsor is North Shore Medical Center. The recorded start is 2006-01, and primary completion is recorded as 2009-05. The phase is listed as NA.

The four groups were hypnotherapy, nicotine replacement therapy, hypnotherapy combined with nicotine replacement, and a self-quit group. The posted primary endpoint results include 41.0 participants in the hypnotherapy arm, 39.0 in the nicotine replacement arm, 38.0 in the combined-treatment arm, and 37.0 in the self-quit arm. These arm figures are not a substitute for a participant flow account: screening, exclusions, withdrawals, and the number assessed at each follow-up are not reported in the registry record.

The hypnotherapy intervention consisted of a 90 minute session within 2 weeks of discharge, a tape for continued use, brochures, and counseling during hospitalization. The nicotine replacement group received a free one month supply, brochures, and counseling during hospitalization and by telephone at 1,2,4,8 and 12 weeks after hospitalization. The combined group received a similar hypnotherapy session and tape, brochure and counseling protocol, and nicotine replacement supplies for a month after discharge. The self-quit group received brief counseling during hospitalization and was not to be contacted until 26 weeks after hospitalization.

How the random sequence was generated, whether allocation was concealed, and whether treatment adherence was measured are not reported in the registry record. No masking was listed, so knowledge of assigned treatment was not masked according to the record. Whether outcome assessors were masked is not reported. The registry does not provide further detail about co-interventions or deviations from the described treatment protocols.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

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

Population: patients included in analysis were less than numbers recruited in groups because some patients were eliminated due to severity of illness including mortality and one developed psychosis, thus became eligible. All patients that were lost to follow up were considered to be smokers for analysis.

6. Primary Endpoint

The registry lists the primary outcome as Abstinence From Smoking, measured over at 26 weeks after hospitalization.

The primary endpoint is abstinence from smoking at 26 weeks after hospitalization, reported as a percentage of participants. The registry defines it as 7-day prevalence of verified tobacco abstinence. Verification was described as biochemical confirmation by urine Cotinine testing or confirmation by telephone and discussion with a household proxy. Participants lost to follow-up were considered to be persistent smokers for this endpoint.

This endpoint captures reported abstinence over a defined period close to the follow-up assessment. It is not a measure of continuous abstinence over the entire period after discharge. The use of biochemical testing or proxy discussion is intended to add verification beyond a participant’s uncorroborated report, although the registry does not report how often each verification route was used, whether the routes were applied consistently across groups, or how discordant information was handled.

General statistical context: A binary endpoint classifies each participant as having or not having the event of interest; the arm percentage describes the observed proportion classified as abstinent. The registry’s rule for loss to follow-up makes the endpoint a combination of observed outcomes and a stated missing-outcome assumption. That convention is important when interpreting the percentages because a participant not reached is counted as smoking rather than omitted from the endpoint denominator. The details of any separate endpoint-specific denominators are not reported in the registry record.

7. Results Posted in the Registry

• Nicotine Replacement Therapy: 7.7% (3/39) versus 14.6% (6/41) on control; risk difference -6.9 percentage points (95% CI -20.6 to 6.7), risk ratio 0.53 (0.14–1.96); unadjusted two-proportion z-test p = 0.326.
• Hypnotherapy and Nicotine Replacement: 13.2% (5/38) versus 14.6% (6/41) on control; risk difference -1.5 percentage points (95% CI -16.7 to 13.8), risk ratio 0.90 (0.30–2.71); unadjusted two-proportion z-test p = 0.850.
• Self-Quit Group: 10.8% (4/37) versus 14.6% (6/41) on control; risk difference -3.8 percentage points (95% CI -18.6 to 10.9), risk ratio 0.74 (0.23–2.42); unadjusted two-proportion z-test p = 0.614.

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.

Smoking Cessation

• 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:
  • Nicotine Replacement Therapy: 28.2% (11/39) versus 43.9% (18/41) on control; risk difference -15.7 percentage points (95% CI -36.4 to 5.0), risk ratio 0.64 (0.35–1.18); unadjusted two-proportion z-test p = 0.144.
  • Hypnotherapy and Nicotine Replacement: 47.4% (18/38) versus 43.9% (18/41) on control; risk difference 3.5 percentage points (95% CI -18.5 to 25.4), risk ratio 1.08 (0.67–1.75); unadjusted two-proportion z-test p = 0.757.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nicotine Replacement Therapy and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hypnotherapy and Nicotine Replacement and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts secondary smoking-cessation outcomes at 12 weeks and smoking abstinence rates at 12 and 26 weeks. Across the reported secondary results, the observed pattern is not uniformly ordered across groups and follow-up assessments. The secondary findings add context to the primary 26-week result, but they do not provide a consistently precise set of contrasts that resolves the uncertainty in the primary comparisons.

The secondary estimates and their uncertainty should be considered alongside the primary endpoint rather than as independent confirmation. The same trial participants and intervention groups contribute to related smoking-cessation outcomes, so findings across follow-up points are not wholly independent pieces of evidence. Differences in the observed pattern across time can reflect the outcome definition, follow-up, or sampling variability; the registry does not report analyses that explain such variation.

Unadjusted secondary comparisons carry less weight for confirmatory interpretation because several outcomes and contrasts create more opportunities for chance findings. The registry record does not report a multiplicity plan, identify a hierarchy among the secondary endpoints, or state which secondary tests were prespecified. It also does not provide enough analytic detail to determine whether the reported secondary results were adjusted for participant characteristics or missing outcomes. These limitations make the secondary findings useful as descriptive context, but not a basis for overriding the uncertainty in the primary result.

Interpretation is further limited because the registry’s secondary outcome list and posted results do not provide a complete account of how each outcome was measured or how participants with missing follow-up were handled. The primary endpoint’s rule for loss to follow-up is stated, but whether that same rule was applied to every secondary measure is not reported in the registry record.

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

• Smoking Cessation
• Smoking Abstinence Rate at 12 and 26 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical context: The primary outcome is binary: each participant is classified according to whether abstinence was verified at the assessment. A percentage summarizes the share classified as abstinent within an arm. A risk difference expresses the difference between two such proportions. In these recalculations, the other arm is compared with hypnotherapy; a negative estimate corresponds to a lower observed abstinence proportion in the comparison arm. This effect measure is expressed on an absolute scale, so it describes percentage-point differences rather than a relative multiple.

The posted risk-difference estimates are unadjusted recalculations from the arm-level summary data. They are not adjusted for participant characteristics or other variables. The registry does not report an adjusted primary model or the sponsor’s statistical method for the primary endpoint. The calculated p-values are likewise unadjusted. A p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the test; it is not the probability that the null hypothesis is true, and it does not describe the size or clinical importance of a difference.

General statistical context: A confidence interval gives a range of effect values reasonably compatible with the data under the method used to construct it. It is not a guarantee that the true effect lies in that interval, and it does not resolve limitations in the study design or measurement. For a risk difference, zero represents no difference. Each recalculated primary interval includes zero, leaving the direction and magnitude uncertain. Interval width matters: a broad interval can encompass meaningfully different effects even if a point estimate is near zero.

The record also lists risk ratios and odds ratios in the recalculated comparisons. A risk ratio compares the proportions in relative terms, while an odds ratio compares the odds of the outcome. These relative measures answer a different scale of question from the risk difference. The registry’s sponsor-reported analyses use risk ratios for two pairs of groups, but the analysis method is not specified. The sponsor-reported ratios should therefore be distinguished from the unadjusted risk-difference recalculations rather than combined as if they were one analysis.

The primary endpoint treats loss to follow-up as persistent smoking. This is an explicit missing-outcome convention for the primary measure, not evidence that every missing participant was smoking. Such a convention can influence the observed outcome proportions if follow-up differs by group. The record does not report follow-up completeness by arm or sensitivity analyses under other missing-data assumptions. Analysis populations, including whether all randomized participants were included as assigned, are not reported in the registry record.

Several important design and analysis details are also absent. The registry does not report the random-sequence method, allocation concealment, endpoint assessor masking, a prespecified analysis plan, covariate adjustment, or the handling of protocol deviations. The trial’s original sample-size justification and assumptions are not reported in the registry record. The separate planning illustrations use stated assumptions based on the observed effect and should not be mistaken for evidence that the trial was designed with those assumptions.

General statistical context: Over-dispersion is a concern when observed variation is greater than a model assumes, particularly in settings with clustered observations or repeated measures. The primary outcome is recorded as a participant-level binary result; the registry does not describe a clustered or repeated-measures model, and it does not report an over-dispersion assessment. It would therefore be inappropriate to infer that such a model was used or that a particular dispersion adjustment was needed.

The reported primary comparisons involve several arms, and secondary outcomes are also posted. Testing multiple comparisons increases the chance of a chance finding if each test is interpreted in isolation. A prespecified multiplicity procedure can address that issue, but none is reported in the registry record. The displayed p-values are unadjusted and should be read as exploratory evidence alongside the effect estimates and confidence intervals, not as a complete account of uncertainty across all analyses.

The registry’s reported analyses do not include p-values for the sponsor’s risk-ratio results, and the method field is not specified. No interim analyses, stopping rules, or monitoring plan are reported in the registry record. These absences limit reconstruction of the full statistical plan and make it important to separate what is directly reported from what can be recalculated from the posted arm summaries.

11. Confidence Intervals and Precision

The primary recalculated risk-difference intervals are wide. For nicotine replacement therapy versus hypnotherapy, the estimate is -0.069 and its 95% confidence interval extends from -0.206 to 0.067. For hypnotherapy plus nicotine replacement versus hypnotherapy, the estimate is -0.015, with a 95% confidence interval from -0.167 to 0.138. For self-quit versus hypnotherapy, the estimate is -0.038, with a 95% confidence interval from -0.186 to 0.109. Each range includes zero and includes values on both sides of zero.

General statistical context: The point estimate is a single summary of the observed contrast, while the confidence interval communicates how much uncertainty remains around that estimate. An interval that includes zero does not prove there is no difference. It means the observed data, analyzed by this unadjusted method, do not narrowly pin down the difference’s direction. The broad ranges also mean that the data are compatible with more than a small difference; the estimates should not be read as precise measurements of the underlying effect.

The sponsor-reported risk ratios also have broad intervals: 2.6 (95% CI 1.1 to 11.4) for the hypnotherapy and nicotine replacement pair, and 2.4 (95% CI 1.04 to 9.7) for the nicotine replacement and combined-treatment pair. These intervals are on a relative scale and are not interchangeable with the recalculated risk-difference intervals. Their analysis method is not reported in the registry record.

Confidence intervals describe sampling uncertainty under their statistical assumptions; they do not account for every source of uncertainty. They cannot resolve the unreported details of outcome ascertainment, missingness by arm, or the analysis plan. In particular, the primary missing-outcome rule counts participants lost to follow-up as persistent smokers, but the record does not provide follow-up completeness or sensitivity analyses. Precision should therefore be understood as precision around the calculated contrast, not as a guarantee that all study uncertainties have been captured.

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 assumptions. The original sample-size justification and assumptions are not reported in the registry record. The listed assumptions for the illustrations are 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 to be detected. For these non-time-to-event outcomes, the figures are participants per arm, not a total across arms or a total number of events.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% probability of detecting the stated effect under those assumptions. The 90% power column describes the corresponding number per arm for a 90% probability. In plain terms, the higher target probability requires a larger planned sample for the same assumed effect. For each comparison, the figures also rise as the planning effect is reduced from 100% to 75% to 50% of the observed effect: smaller effects are harder to distinguish from random variation and therefore require more participants under the stated assumptions.

These calculations are planning illustrations, not observed power. They do not show the probability that the completed trial’s result is correct, and they do not establish whether the trial’s original design was adequate. Because the observed contrasts are uncertain, using them as the basis for planning can produce unstable illustrations. A future design would need its own clinically justified target effect and design assumptions; those choices are not specified in the registry record.

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 = 0.146; treatment proportion p₁ = 0.077; average p̄ = 0.112.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4454 = 0.8729.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4426 = 0.3725.
4. n = (0.8729 + 0.3725)² / (-0.0694)² = 321.9, rounded up to 322 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 <- 0.146341463414634                          # control proportion
p1 <- 0.0769230769230769                          # 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(1791803)
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 = 322 (80% power), 431 (90% power)
 75% of observed effect: n per arm = 612 (80% power), 819 (90% power)
 50% of observed effect: n per arm = 1,463 (80% power), 1,958 (90% power)
power.prop.test: 321.9 
Simulated power at n = 322 per arm: 0.805 (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 two sponsor analyses using risk ratios. For the hypnotherapy and nicotine replacement groups, the reported risk ratio is 2.6, with a 95% confidence interval from 1.1 to 11.4. For the nicotine replacement and hypnotherapy-plus-nicotine-replacement groups, the reported risk ratio is 2.4, with a 95% confidence interval from 1.04 to 9.7. The registry does not state the method used or report p-values for these analyses.

The recalculated primary comparisons instead use unadjusted risk differences, comparing each of the three other arms with hypnotherapy. They are straightforward recalculations from the posted summary statistics, not a reproduction of a documented sponsor model. A risk ratio and a risk difference use different scales, and the sponsor’s reported group pairs do not cover exactly the same set of contrasts as the recalculations. Their point estimates and intervals should therefore be read as separate analyses rather than treated as directly interchangeable.

The discrepancy flag is false, so no reported discrepancy is identified between the sponsor analysis and the recalculation. That does not establish that the methods are identical: the sponsor’s analytic details are not reported in the registry record. The sponsor’s own analysis is the source for its reported results; the recalculated estimates are best understood as supplementary, unadjusted comparisons based on the posted arm summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry includes a primary endpoint, secondary outcomes, and multiple arm comparisons. It reports six analyses in total, but does not describe a prespecified testing hierarchy or a method for controlling the chance of false-positive findings across analyses. The recalculated p-values are unadjusted. Without a reported multiplicity plan, individual p-values should not be interpreted as if they were the only tests conducted.

Missing data are addressed explicitly for the primary endpoint: participants lost to follow-up were considered to be persistent smokers. This is a stated classification rule, not a report that no one was lost or that missingness was inconsequential. Follow-up rates by group, reasons for loss, and sensitivity analyses using alternative assumptions are not reported in the registry record. Handling of missing data for the secondary endpoints is also not reported.

The record does not state the analysis population used for the sponsor’s analyses or whether all randomized participants were analyzed in their assigned groups. It does not report exclusions after randomization, treatment adherence, crossover, or protocol deviations. As a result, the posted group summaries do not establish which analysis population generated every reported result.

Other elements needed to evaluate the statistical plan are not reported in the registry record, including random-sequence generation, allocation concealment, outcome assessor masking, covariate adjustment, interim analyses, and stopping rules. The method for the sponsor’s reported risk ratios is not reported. These gaps do not invalidate the posted descriptive outcomes, but they limit assessment of bias, multiplicity, and the assumptions behind inferential results.

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 0% reporting threshold.

The registry reports zero serious adverse events in each group, and zero other adverse events in each group. The number at risk is listed as 41 for hypnotherapy, 39 for nicotine replacement therapy, 38 for the combined group, and 37 for self-quit for both serious and other adverse events. Death counts are null, so deaths are not reported in the registry record. No serious adverse event terms are listed.

These entries describe what the registry reports; they do not establish that no adverse events occurred outside the recorded categories or reporting process. The record does not give definitions of serious or other adverse events, collection procedures, follow-up duration for safety, or detail about whether events were assessed systematically. Zero recorded events should therefore be read as zero reported in these fields, not as proof of no risk. The safety information is limited and does not support a comparative safety conclusion.

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

The primary results show the observed abstinence percentages for each randomized group at 26 weeks after hospitalization. In this trial record, the hypnotherapy arm had the highest posted percentage, while the other arms had lower percentages. The unadjusted risk-difference estimates are uncertain: every primary interval includes zero and spans effects in both directions. Thus, the posted results do not precisely determine the differences among these groups.

This is not the same as demonstrating that all approaches produce equivalent outcomes. Equivalence or non-inferiority requires a prespecified margin and an analysis designed to assess that question; neither is reported in the registry record. Likewise, a confidence interval that includes zero is not proof that there is no effect. The results are compatible with a range of possible differences, and the trial’s precision is limited.

The endpoint concerns verified 7-day abstinence at a specific follow-up after hospitalization, not continuous abstinence throughout the entire period. Participants lost to follow-up were counted as persistent smokers for the primary endpoint. The record does not provide follow-up completeness by group or sensitivity analyses that would show how alternative missing-data assumptions could affect the results.

The evidence should be interpreted within the population and interventions described in the registry. Further eligibility details, participant characteristics, and information about treatment adherence are not reported. The registry’s sponsor analyses and the supplementary recalculations also use different effect measures and group contrasts, so they are not interchangeable summaries.

These findings do not establish what would occur in other populations, with different cessation programs, or beyond the reported follow-up. They are a record of observed outcomes and uncertain comparisons, not medical advice or a definitive ranking of approaches.

18. Why This Trial Matters Statistically

This trial illustrates why an observed difference and evidence of a precise difference are not the same thing. The arm percentages provide an intuitive description of the outcomes, while the risk-difference intervals show that the data leave considerable uncertainty about the contrasts. Reporting both helps prevent a ranking of point estimates from being mistaken for a reliable ordering of treatments.

It also shows how endpoint rules shape interpretation. The primary outcome is a verified 7-day abstinence measure, and participants lost to follow-up were classified as persistent smokers. That explicit rule is useful to know, but without group-specific follow-up information and sensitivity analyses, readers cannot judge how robust the comparisons are to missing-outcome assumptions.

The record makes a distinction between sponsor-reported risk ratios and unadjusted recalculated risk differences especially important. Different effect measures answer different questions, and comparisons involving different pairs of groups do not constitute one unified analysis. Statistical interpretation depends on identifying the contrast, scale, and method behind each estimate.

Finally, planning illustrations based on the observed effect are not evidence about the design of the completed trial. The record’s lack of an original sample-size justification, a reported multiplicity strategy, and further analysis details limits retrospective evaluation of design choices. These are practical lessons for interpreting registry results: keep descriptive findings, inferential estimates, and planning calculations separate, and give the uncertainty and reporting gaps equal attention.

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.

Several limitations specific to this trial affect interpretation. The primary endpoint combines a biochemical verification route with telephone discussion with a household proxy, but the registry does not report how often each route was used or whether ascertainment differed by group. The extent to which the verification process was applied consistently is therefore unclear.

The treatment groups differed in contact and follow-up descriptions. The nicotine replacement group was to receive telephone counseling at 1,2,4,8 and 12 weeks, while the self-quit group was not to be contacted until 26 weeks after hospitalization. The registry does not report actual contact, adherence, or whether the planned procedures were delivered as described. With no masking listed, participants and treatment providers could have known group assignment; whether outcome assessors were masked is not reported.

The primary result is based on a relatively small set of participants in each arm, and the recalculated intervals are broad. The registry does not report the method of random sequence generation or allocation concealment, participant characteristics, baseline comparability, or a detailed participant flow. These omissions limit assessment of selection processes and the comparability of groups after randomization.

There is also limited information about the analysis plan. The method for sponsor-reported risk ratios, the analysis population, any covariate adjustment, the multiplicity strategy, and sensitivity analyses are not reported in the registry record. The primary missing-data rule is stated, but completeness by arm and handling of missing secondary outcomes are not. These limitations do not change the reported outcomes, but they constrain how confidently differences can be attributed to the interventions or generalized beyond the recorded trial population.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Smoking Cessation After Hospitalization for a Cardiopulmonary Illness — NCT01791803.
• Registry record last updated 2017-05-19; status last verified 2017-05.
• Results first posted 2017-05-19.
• 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 registry record describes a completed randomized, parallel-group trial with no masking, sponsored by North Shore Medical Center. It compared hypnotherapy, nicotine replacement therapy, their combination, and a self-quit approach among hospitalized patients with a cardiopulmonary illness who smoked.

The primary endpoint was verified 7-day smoking abstinence at 26 weeks after hospitalization. The posted arm percentages were 15.0 for hypnotherapy, 7.0 for nicotine replacement therapy, 13.0 for the combined group, and 10.0 for self-quit. Unadjusted recalculated risk differences had broad confidence intervals that included zero. Sponsor-reported risk ratios are also listed for two group pairs, but their methods are not reported.

The primary missing-outcome rule classified participants lost to follow-up as persistent smokers. The record does not report an original sample-size justification, multiplicity plan, analysis population, or several design and analysis details. The results are therefore best read as descriptive outcomes with substantial uncertainty, not as a definitive ranking of cessation approaches.