An Innovative Conversational Agent (Quitbot) for Smoking Cessation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Innovative Conversational Agent (Quitbot) for Smoking Cessation (NCT04308759), a randomized na study. The primary outcome is Number of Participants With 30-day Cigarette Smoking Cessation.

2. Clinical Question

The question is framed around 30-day point prevalence abstinence rather than continuous abstinence throughout the follow-up period. A participant qualifies for the primary outcome when their answer indicates that their last cigarette was more than 30 days earlier. The record says missing primary outcome data are coded as smoking under an intent-to-treat approach. This makes the handling of missing outcomes part of the endpoint definition and interpretation.

The trial record describes a randomized comparison of remote digital programs. It does not report a population description beyond the smoking-cessation condition and the outcome information. Specific eligibility details and further participant characteristics are not reported in the registry record.

3. Trial Design

The registry record describes a randomized, double-masked, parallel-group trial. Participants were assigned to one of two remote digital smoking cessation programs: QuitBot or SmokefreeTXT. The record lists enrollment of 1647 and the status as completed. The record gives a start date of 2022-07-24 and a primary completion date of 2025-05-01. Its formal phase entry is NA, while the brief summary describes the study as a phase III trial.

Both programs were delivered remotely for 42 days. QuitBot was a smartphone chatbot application, and SmokefreeTXT was a text messaging program described as standard of care. The registry record identifies the trial as parallel-group, meaning the reported comparison is between separate groups assigned to different programs, rather than a within-participant comparison of both programs.

The primary outcome was assessed at 12 months after randomization. The recorded endpoint was the number of participants with 30-day cigarette smoking cessation, defined by the question about when the participant last smoked or tried a cigarette. A response indicating no cigarette use in the past 30 days counted as abstinent. The record also posts a secondary result for the same abstinence outcome at 6 months after randomization.

The record reports the numbers analyzed for the outcome groups: 826 in SmokefreeTXT and 821 in QuitBot. These are the group sizes shown with the posted primary outcome. The record’s description of missing primary outcome handling says missing data were coded as smoking in a standard intent-to-treat analysis. Other details about the original sample-size rationale, randomization procedures, masking procedures, adherence, or analysis populations are not reported in the registry record.

Allocation is listed as randomized and masking as double, but the record does not explain which people were masked or how masking was maintained for remote programs. The registry information therefore supports a broad description of the design, not a detailed reconstruction of all trial procedures.

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.

3-Month Follow-up Survey

Reasons for not completing this period:

6-Month Follow-up Survey

Reasons for not completing this period:

12-Month Follow-up Survey

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 Number of Participants With 30-day Cigarette Smoking Cessation, measured over At 12 months after randomization.

The primary endpoint is the number of participants with 30-day point prevalence abstinence from cigarette smoking at 12 months after randomization. Participants were asked when they last smoked, or even tried, a cigarette. The response options were Earlier today, 24 hours ago, 2-7 days ago, 8-30 days ago, and Over 30 days ago. Those reporting no cigarette consumption in the past 30 days were counted as abstinent.

This endpoint captures reported smoking status over a defined recent period at a particular follow-up assessment. It is not a measure of uninterrupted abstinence across the full time since randomization. That distinction matters: a participant’s classification reflects the answer about the preceding 30 days, not a complete record of smoking behavior throughout follow-up.

Counting participants with the outcome makes the endpoint binary at the participant level: each participant is classified as abstinent or not abstinent according to the stated rule. The group summaries report the count and group size, while the comparative analyses express the between-group contrast on different statistical scales. The endpoint is used to make the outcome definition explicit and apply it consistently across the randomized groups.

The record states that missing primary outcome data are handled using a standard intent-to-treat analysis, with missing observations coded as smoking. This is a conservative classification for the abstinence outcome, but the registry record does not report how many outcomes were missing or provide further details about the handling of missingness at other time points. It also does not report a separate verification procedure for self-reported abstinence.

7. Results Posted in the Registry

• Group I (QuitBot Experimental): 22.7% (186/821) versus 23.1% (191/826) on control; risk difference -0.5 percentage points (95% CI -4.5 to 3.6), risk ratio 0.98 (0.82–1.17); unadjusted two-proportion z-test p = 0.821.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With 30-day Cigarette 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:
  • Group I (QuitBot Experimental): 18.6% (153/821) versus 19.2% (159/826) on control; risk difference -0.6 percentage points (95% CI -4.4 to 3.2), risk ratio 0.97 (0.79–1.18); unadjusted two-proportion z-test p = 0.751.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group I (QuitBot Experimental) and the control. The interval gives the range of effects that remain compatible with the data.

The registry record posts one secondary outcome: the same 30-day cigarette smoking cessation measure assessed at 6 months after randomization. The broad pattern is consistent with the primary comparison in that the posted secondary analysis also does not establish a statistically clear separation between the assigned programs. The secondary result can add context about the outcome at an earlier follow-up, but it does not replace the primary assessment at 12 months.

The secondary endpoint uses the same stated abstinence concept, but its timing differs. A result at an earlier assessment and a result at the primary assessment describe outcome status at different points in follow-up. They should not be treated as repeated measurements of one unchanged state, or as evidence about continuous abstinence across the period.

The secondary analysis is a complementary finding, not an independent confirmation in the strongest sense. The same participants and outcome framework may contribute to both assessments, and the registry record does not report an analysis plan describing how these outcomes were to be combined or prioritized. The record lists one secondary outcome, but does not report how multiplicity across the primary and secondary analyses was handled.

Unadjusted secondary results generally carry less weight than the prespecified primary analysis because they may be less central to the study’s main question and can be more exposed to selective emphasis when multiple outcomes or time points are examined. The registry record does not report whether this secondary outcome was prespecified in the original protocol or whether adjustment for multiple comparisons was planned. Accordingly, the secondary pattern is useful context, but should not be used alone to make a definitive claim about the programs.

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

• Number of Participants With 30-day Cigarette Smoking Cessation

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute?

Random assignment is intended to make the treatment groups comparable, on average, with respect to factors that could affect the outcome. It provides a basis for comparing the observed outcome summaries between assigned groups. Randomization does not guarantee that every characteristic is perfectly balanced, and the registry record does not report detailed baseline characteristics. The record identifies the trial as randomized, but does not give further details about the sequence generation or allocation concealment.

The parallel-group design means that participants were assigned to one program group for the comparison. The posted primary result is therefore a comparison of the QuitBot group with the SmokefreeTXT group at the stated assessment, rather than a comparison of each participant with their own outcome under both programs.

What is a binary outcome?

The primary outcome counts participants classified as abstinent under the stated 30-day definition. At the participant level, the classification is binary: the participant either meets the definition or does not. Group counts can be summarized as proportions, and comparative methods can express the contrast as a difference in proportions or as an odds ratio. These measures answer related but not identical questions and have different numerical scales.

The recalculated risk difference is an unadjusted contrast in the group proportions, expressed as QuitBot minus SmokefreeTXT. A value near zero indicates that the observed proportions are close on this scale. The confidence interval describes a range of values compatible with the data and the calculation’s assumptions. The interval is not a guarantee that the true effect lies within it, nor does it assign a probability to a particular effect after observing the data.

Why can analyses use different effect measures?

The registry’s reported analysis uses logistic regression and reports an odds ratio. An odds ratio compares the odds of the outcome between groups; it is not the same as a risk difference, which compares proportions by subtraction. Logistic regression can be used to model a binary outcome, and covariates may be included in such a model, but the registry record does not report whether covariates were included in this analysis. It is therefore safest to describe the posted method and estimate without assuming a particular adjustment set.

The recalculated analysis is a simple unadjusted calculation from the posted group counts. It offers a transparent comparison based on the summaries, but it is not a replacement for the sponsor’s reported analysis. The reported analysis takes precedence as the sponsor’s own inferential analysis; the recalculation is a complementary way to understand the posted data on another scale. The record does not flag a discrepancy between the two.

How should the p-values be understood?

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model. It is not the probability that the null hypothesis is true, and it does not describe the size or practical importance of an effect. The recalculated p-value is 0.821, and the sponsor’s reported p-value is 0.720. Both are consistent with the corresponding confidence intervals including the null value for the reported comparison, but neither establishes that the groups are identical.

The registry describes the reported analysis as a superiority analysis. A superiority test assesses evidence for a difference under its specified model and analysis. Failure to find statistically clear evidence of superiority does not demonstrate equivalence or non-inferiority. Those conclusions require an appropriate framework and prespecified margins, which are not reported in the registry record.

What does the confidence interval add?

A confidence interval conveys uncertainty around an estimated contrast. A narrower interval indicates greater statistical precision under the method used; a wider interval leaves more possible effect sizes compatible with the data. For the primary recalculation, the interval ranges from -0.045 to 0.036. Because it spans values on both sides of zero, the data are compatible with a modest difference favoring either group as well as a value near no difference on this scale.

Confidence intervals are affected by the amount of information in the data, the variability of the outcome, and the statistical method. A result can have a small point estimate but still be uncertain, or a larger estimate with an interval that remains broad. Interpretation should therefore consider the estimate and its interval together rather than relying only on a p-value.

Why does missing-data handling matter?

The primary endpoint description says missing outcomes are coded as smoking in a standard intent-to-treat analysis. This rule preserves participants in the assigned-group comparison and makes explicit how missing responses contribute to the abstinence count. It also means that the analysis treats a missing outcome as not abstinent, regardless of the participant’s unobserved smoking status. The number of missing primary outcomes and any sensitivity analyses are not reported in the registry record.

Intent-to-treat generally refers to analyzing participants according to their randomized assignment, but the exact analysis population and implementation details are not reported beyond the missing-as-smoking description. The registry does not report whether all randomized participants posted follow-up data, or how missingness was addressed for the secondary outcome.

What can planning calculations tell us?

The sample-size illustrations use the observed effect as a reference and show the participants per arm associated with different assumed fractions of that effect. They are planning calculations, not a reconstruction of the original trial design and not evidence that the observed study had a particular probability of detecting an effect. The record’s listed calculation assumptions are described in the sample-size section. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.005, with a confidence interval from -0.045 to 0.036. The point estimate is close to zero, but the interval is not concentrated at a single value. It includes zero and allows for differences in either direction. That is why the estimate is best read as an imprecise comparison that does not show a clear group separation, rather than as evidence that the programs have exactly the same outcome.

The sponsor’s logistic-regression estimate is an odds ratio of 0.96, with a 95% confidence interval from 0.76 to 1.21. This interval includes the odds-ratio null value of 1. The confidence interval and p = 0.720 indicate that the reported analysis does not establish a statistically clear difference. Since the reported odds ratio and the recalculated risk difference are on distinct scales, their interval endpoints cannot be compared directly.

A confidence interval summarizes uncertainty under a statistical procedure and its assumptions. It is not a range that guarantees the underlying effect must occupy those values. Nor does an interval containing a null value prove no effect. In this trial, the interval permits a range of possible group differences, so conclusions about the size and direction of any underlying difference remain limited.

Precision depends not just on the number of participants, but also on the number of outcome events and the method used. The posted group sizes are 826 for SmokefreeTXT and 821 for QuitBot. Those enrollment figures should be considered alongside the observed outcome counts and the width of the interval. The registry record does not provide a separate precision target or a clinically important difference threshold, so the interval cannot be judged against a prespecified threshold for meaningful benefit.

The arm-level intervals shown with the primary results also overlap. Overlap alone is not a formal test of the between-group contrast; the direct comparative interval is the more appropriate summary for that question.

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 sample-size table and curve are planning illustrations based on the observed effect, not the original design calculation. For this binary outcome, the table reports participants per arm, not total events. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size justification and design assumptions are not reported in the registry record.

The column for 80% power shows the participants per arm associated with an 80% probability of detecting the assumed effect under those planning assumptions, if the assumed effect and model are correct. The 90% power column uses a higher target probability of detecting that effect, and therefore generally calls for a larger planned sample. These are design-planning quantities; they are not estimates of the probability that this completed trial detected an effect. This is not observed power.

The table includes planning for 100%, 75%, and 50% of the observed effect. Planning for a smaller effect requires more participants because smaller differences are harder to distinguish from random variation. The figures become very large when the assumed effect is a reduced fraction of the observed estimate, reflecting the difficulty of reliably detecting a small difference with this design and outcome.

The illustrations should not be read as a recommendation or as a claim that the trial was under- or over-sized relative to its original plan. They apply the stated general assumptions to the observed effect, and the record does not report whether the original trial used the same assumptions. The curve is another presentation of the planning calculations, not independent evidence about the trial’s outcome.

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 = 0.231; treatment proportion p₁ = 0.227; average p̄ = 0.229.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5941 = 1.1645.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5941 = 0.5000.
4. n = (1.1645 + 0.5000)² / (-0.0047)² = 126,398.2, rounded up to 126,399 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 <- 0.231234866828087                          # control proportion
p1 <- 0.226552984165652                          # 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(4308759)
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 = 126,399 (80% power), 169,211 (90% power)
 75% of observed effect: n per arm = 225,113 (80% power), 301,362 (90% power)
 50% of observed effect: n per arm = 507,411 (80% power), 679,279 (90% power)
power.prop.test: 126398.2 
Simulated power at n = 126,399 per arm: 0.804 (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 posted primary analysis is logistic regression, reporting an odds ratio of 0.96, a 95% confidence interval from 0.76 to 1.21, and p = 0.720. The recalculation uses the posted group counts to estimate an unadjusted risk difference of -0.005, with a confidence interval from -0.045 to 0.036 and p = 0.821. Both analyses describe a comparison without statistically clear evidence of a difference, but they report distinct effect measures and are not numerically interchangeable.

The sponsor’s analysis is the trial’s own reported inferential analysis. The recalculation is useful as a transparent, unadjusted summary based on the group counts and helps readers see the comparison on the risk-difference scale. The registry record does not flag a discrepancy between the sponsor analysis and recalculation. The methods differ, so modest differences in estimates, intervals, and p-values are not in themselves contradictory.

The registry record does not report whether the logistic regression adjusted for covariates, nor does it give further details of its model specification. Those details should not be inferred from the method label alone. The sponsor result should be interpreted as the reported analysis, while the recalculation should remain clearly identified as an unadjusted re-analysis of summary data.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity adjustment or a broader testing strategy for the primary and secondary outcomes. The posted results include the primary outcome at 12 months and a secondary outcome at 6 months, each assessed as 30-day cigarette smoking cessation. When several outcomes or assessment times are examined, the chance of obtaining an apparently notable result by chance can increase. A prespecified hierarchy or adjustment can address this concern, but the registry record does not say whether either was used.

The sponsor describes the primary result as a superiority analysis, but the registry record does not report a full statistical analysis plan, the planned significance threshold for the sponsor analysis, or whether analyses were prespecified in a protocol. Planning assumptions for the sample-size illustration are listed separately, but those are not evidence of the trial’s original analysis plan.

For the primary outcome, the record states that missing data were handled using standard intent-to-treat analysis, with all missing data coded as smoking. This is an explicit rule that counts missing outcomes as non-abstinent. However, the number of missing outcomes is not reported in the registry record, and the record does not describe sensitivity analyses that might show how conclusions would change under different assumptions about missing outcomes.

The missing-data rule is not described for the secondary result. The registry record also does not report a detailed analysis population definition, such as whether the reported group sizes include every randomized participant or how any departures from assigned treatment were handled. Although the randomized groups and outcome denominators are posted, further information about exclusions, adherence, or the use of an intention-to-treat population is not reported in the registry record.

These reporting gaps do not invalidate the posted findings, but they limit the ability to assess the full analytic context. Interpretation should therefore distinguish the explicit primary missing-data rule from other analysis details that are not reported.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The posted safety figures list 821 participants at risk in the QuitBot group and 826 at risk in the SmokefreeTXT group. For both groups, the registry record reports 0 serious adverse events, 0 other adverse events, and 0 deaths. These entries describe the counts recorded in the registry’s safety section.

Zero events in the posted figures means no events of those listed types were recorded in the reported safety summary. It does not establish that no unwanted experiences occurred outside the categories or reporting process represented there. The registry record does not provide a list of serious adverse event terms, and the serious-event term list is empty. It also does not provide further detail about event definitions, collection procedures, or attribution to a program.

These figures should be read as descriptive safety reporting, not as a comparative test of safety. The record does not report an analysis of between-group safety differences. As with any registry summary, absence of a recorded event is not proof that the risk is zero; it indicates what the posted safety figures show.

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

The posted primary results show similar observed abstinence counts and proportions across the two groups at the 12-month assessment, with a recalculated risk-difference estimate close to zero. The sponsor’s logistic-regression analysis also does not show statistically clear evidence of a difference. The intervals remain compatible with differences in either direction, so the result should be described as inconclusive about a precise between-program difference rather than as proof that the programs are identical.

The outcome is 30-day point prevalence abstinence, based on participants’ answers at a follow-up assessment. It does not measure continuous abstinence throughout the period after randomization. The registry record does not report biochemical confirmation of participants’ self-reports. The primary missing-data rule counts missing outcomes as smoking, but the number of missing outcomes is not reported.

The findings concern the specific programs and trial comparison described in the record: a 42-day QuitBot program compared with a 42-day SmokefreeTXT program. They do not establish how other versions of the programs, different delivery arrangements, or different groups of participants would compare. The record lists randomization and double masking, but details about masking implementation and participant characteristics are not reported in the registry record.

A result without statistically clear evidence of superiority does not establish equivalence or non-inferiority. Those claims require a design and analysis intended to test a defined margin, which is not reported. Likewise, the posted results do not show that either program works or fails in a general clinical sense. They describe the outcome comparison observed in this trial and the uncertainty around it.

The most defensible reading is therefore limited and specific: the posted analyses do not identify a clear difference between groups at the primary assessment, while the confidence intervals leave meaningful uncertainty about the size and direction of the underlying contrast.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two active remote smoking-cessation programs rather than contrasting a program with no intervention. The interpretation is consequently about the relative outcome observed between QuitBot and SmokefreeTXT, not about the effect of receiving any support compared with receiving none. The comparator’s description as standard of care is part of the registry record and helps define the practical comparison being made.

The trial also illustrates why a point estimate alone is insufficient. The primary risk-difference estimate is close to zero, while its confidence interval permits a range of effects in either direction. Reporting both the estimate and its uncertainty prevents a near-zero point estimate from being mistaken for proof of no possible difference.

The example also shows why effect measures need to be named clearly. The sponsor reports an odds ratio from logistic regression, while the recalculation reports a risk difference from the posted counts. Both address the group comparison, but they represent it on different scales. Readers should not expect their numeric values to match or interpret them as interchangeable.

Finally, the study highlights the difference between trial results and planning illustrations. The sample-size calculations use the observed effect under stated assumptions; they do not establish the trial’s original design rationale or its observed power. Separating those planning quantities from the actual trial analysis helps avoid overstating what can be concluded from retrospective calculations.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report detailed participant characteristics, eligibility criteria, or the settings from which participants were recruited. Without those details, it is difficult to assess how closely the enrolled group reflects other populations of people seeking smoking cessation support. The record gives the program descriptions and outcome definition, but not the full context needed to judge generalizability.

The primary outcome is based on self-report at a single follow-up assessment and represents 30-day point prevalence abstinence. The registry record does not report biochemical validation or continuous abstinence. The endpoint therefore answers a specific question about reported recent smoking, not every possible measure of cessation.

The registry record does not report adherence to the 42-day programs, engagement with the chatbot or text messages, or exposure to other cessation support. These details could help explain outcomes, but should not be assumed. Nor does the record describe which people were masked or how masking was implemented for the digital interventions.

The reported analysis details are limited. The sponsor reports logistic regression but the registry record does not state whether covariates were included, provide a full statistical analysis plan, or explain the analysis population beyond the primary missing-as-smoking rule. The number of missing primary outcomes and sensitivity analyses are not reported. The approach to missing data for the secondary outcome is also not reported.

The registry record does not report how multiplicity was handled across the posted outcome assessments, or the original sample-size justification. The planning calculations are illustrations based on the observed effect and stated assumptions, not evidence about the original design. These limitations counsel against broad claims, while leaving the posted randomized comparison and its stated outcome definition interpretable on their own terms.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: An Innovative Conversational Agent (Quitbot) for Smoking Cessation — NCT04308759.
• Registry record last updated 2026-05-22; status last verified 2026-05.
• Results first posted 2026-05-22.
• 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

This completed randomized, double-masked, parallel-group trial compared two remote smoking cessation programs: QuitBot and SmokefreeTXT. The programs were delivered for 42 days. The registry record lists enrollment of 1647 and a primary completion date of 2025-05-01.

The primary outcome was 30-day cigarette smoking cessation at 12 months after randomization, defined from participants’ reports of when they last smoked or tried a cigarette. Missing primary outcome data were coded as smoking. The posted primary results and sponsor logistic-regression analysis do not establish a statistically clear difference between groups; the recalculated confidence interval permits differences in either direction.

The record also posts the same cessation outcome at 6 months as a secondary result. Safety figures list zero serious adverse events, zero other adverse events, and zero deaths in each group. Further details about the original sample-size rationale, analysis plan, participant characteristics, and several implementation and missing-data questions are not reported in the registry record.