Research and Innovation to Stop E-cigarette/Vaping in Young Adults: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Research and Innovation to Stop E-cigarette/Vaping in Young Adults (NCT04974580), a randomized phase 4 study. The primary outcome is 7-day Point Prevalence Vaping Abstinence.

2. Clinical Question

The planned factorial structure is useful because it separates two intervention components—digital support and NRT—while retaining a common phone-counseling background. The posted primary comparisons are each against the phone-coaching-only group. They therefore describe those assigned groups relative to that reference, rather than establishing every possible interaction or component effect. The registry record does not report the detailed analysis plan needed to determine how the component-level questions were ultimately modeled.

3. Trial Design

This was a randomized, single-masked, phase 4 trial with a factorial model. Enrollment was 508, and the registry status is completed. The study dates recorded are 2021-07-28 for start and 2022-12-30 for primary completion. Ohio State University is listed as sponsor. The trial examined cessation support for young adults who vape, with conditions listed as nicotine dependence and e-cigarette use.

The design is described as 2x2. Its two factors were digital cessation support and NRT: participants could receive neither, digital support alone, NRT alone, or both. Phone counseling was common to all four groups. The coaching-only group received two phone counseling calls; the other groups received those calls in addition to their assigned components. The digital component involved text messages with links to online cessation materials, and the NRT component was nicotine replacement therapy. The registry does not report the masking details or identify which participants or study staff were masked.

The primary outcome was assessed 3 months after the first coaching call, which occurred at baseline. The recorded endpoint is the number of participants reporting no e-cigarette use in the past 7 days at the 3-month survey. The primary population includes participants fully enrolled at baseline, and missing outcomes were imputed as not abstinent. The posted data also include secondary outcomes concerning vaping abstinence, e-cigarette dependence, and changes in use frequency. Although the design structure and broad intervention components are described, the registry record does not report the original sample-size rationale, the detailed randomization procedure, or a complete statistical analysis plan.

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:

Analysis population for the primary outcome, as defined in the registry: All participants who were fully enrolled at baseline are included. Those missing outcome data are imputed as not abstinent.

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 7-day Point Prevalence Vaping Abstinence, measured over 3 months after the first coaching call (occurred at baseline).

The primary endpoint is 7-day point-prevalence vaping abstinence, assessed 3 months after the first coaching call. It counts participants who self-reported no use of e-cigarettes during the 7 days before completing the outcome survey. It is a snapshot of recent use at a defined follow-up, not a measure of uninterrupted abstinence throughout the period since enrollment.

A self-reported point-prevalence outcome gives a clear, time-specific way to compare groups on recent vaping status. It does not, by itself, establish the duration of abstinence, verify reports through a biological measure, or capture changes in use outside the specified 7-day window. Those distinctions matter when interpreting what a group count represents.

The primary population includes everyone fully enrolled at baseline. The registry specifies that participants missing outcome data were imputed as not abstinent. Consequently, the posted primary counts reflect that stated missing-data rule, not only participants who completed the survey and reported their status. This rule makes the outcome definition more explicit, while still leaving questions about the amount and pattern of missingness: those details are not reported in the registry record.

The endpoint is reported as a count of participants rather than a continuous measure. Group sizes differ, so counts should be read alongside the number of participants in each group and the estimated comparisons. A larger count alone does not establish a higher rate when group denominators differ. The statistical comparisons express the observed contrast with the coaching-only group and its uncertainty.

7. Results Posted in the Registry

• DigitalArm: 42.9% (54/126) versus 41.0% (55/134) on control; risk difference 1.8 percentage points (95% CI -10.2 to 13.8), risk ratio 1.04 (0.78–1.39); unadjusted two-proportion z-test p = 0.767.
• CoachingNRTArm: 48.4% (61/126) versus 41.0% (55/134) on control; risk difference 7.4 percentage points (95% CI -4.7 to 19.4), risk ratio 1.18 (0.90–1.55); unadjusted two-proportion z-test p = 0.232.
• DigitalNRTArm: 48.4% (59/122) versus 41.0% (55/134) on control; risk difference 7.3 percentage points (95% CI -4.8 to 19.5), risk ratio 1.18 (0.90–1.55); unadjusted two-proportion z-test p = 0.239.

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.

Vaping Abstinence

• 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:
  • DigitalArm: 35.7% (45/126) versus 34.3% (46/134) on control; risk difference 1.4 percentage points (95% CI -10.2 to 13.0), risk ratio 1.04 (0.75–1.45); unadjusted two-proportion z-test p = 0.815.
  • CoachingNRTArm: 41.3% (52/126) versus 34.3% (46/134) on control; risk difference 6.9 percentage points (95% CI -4.8 to 18.7), risk ratio 1.20 (0.88–1.64); unadjusted two-proportion z-test p = 0.248.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DigitalArm 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 CoachingNRTArm and the control. The interval gives the range of effects that remain compatible with the data.

E-cigarette Dependence - PROMIS-E

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • DigitalArm: mean -2.60 versus -5.50 on control; difference 2.90 (95% CI -1.43 to 7.23), standardized effect d = 0.31; z-test p = 0.190.
  • CoachingNRTArm: mean -6.50 versus -5.50 on control; difference -1.00 (95% CI -5.85 to 3.85), standardized effect d = -0.10; z-test p = 0.686.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DigitalArm 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 CoachingNRTArm and the control. The interval gives the range of effects that remain compatible with the data.

Changes in E-cigarette Use Frequency

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • DigitalArm: mean -6.90 versus -7.90 on control; difference 1.00 (95% CI -3.22 to 5.22), standardized effect d = 0.11; z-test p = 0.642.
  • CoachingNRTArm: mean -9.30 versus -7.90 on control; difference -1.40 (95% CI -5.66 to 2.86), standardized effect d = -0.15; z-test p = 0.519.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DigitalArm 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 CoachingNRTArm and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the view beyond the primary 7-day abstinence definition. The posted outcomes include another vaping-abstinence measure, change in e-cigarette dependence measured with PROMIS-E, and change in vaping days over the past month. Across these measures, the reported estimates vary in direction and precision. Some group summaries are based on substantially smaller participant counts than the primary outcome, and the contrasts generally have appreciable uncertainty.

This pattern does not overturn or independently confirm the primary result. The secondary measures address related but distinct questions: recent abstinence, dependence scores, and frequency of use are not interchangeable endpoints. They can add context about how outcomes may differ across dimensions, but no single one should be treated as a substitute for the registered primary endpoint. The registry also lists a Penn State E-cigarette Dependence Index among the secondary outcomes, but a corresponding result is not included in the posted secondary outcome entries.

The secondary recalculations are unadjusted. When multiple outcomes and comparisons are examined, the chance of at least one apparently notable result can increase. This is a general statistical concern called multiplicity. Without a reported multiplicity strategy, individual secondary p-values should carry less weight than a prespecified primary analysis. The registry record does not report whether adjustments were planned or applied, or how the multiple secondary questions were prioritized.

In combination, the secondary data offer descriptive signals about abstinence, dependence, and use frequency, but they do not yield a single consistent or highly precise account of component effects. Their interpretation should remain exploratory unless the registry record identifies them as confirmatory analyses and documents the relevant analysis plan. Such detail is not reported in the registry record.

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

• Vaping Abstinence
• E-cigarette Dependence - PROMIS-E
• E-cigarette Dependence - Penn State E-cigarette Dependence Index
• Changes in E-cigarette Use Frequency

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint is binary: each participant is classified as abstinent or not abstinent at the 3-month survey. The posted arm results give counts of participants meeting the abstinence definition and the group sizes. A count is not directly comparable across groups of different sizes without accounting for the denominators. The risk difference does this by expressing the difference between the groups’ observed proportions, with a positive estimate indicating a higher observed proportion in the intervention group than in coaching only. These are simple, unadjusted recalculations from the posted summaries.

What does the confidence interval describe?

A confidence interval describes the range of effect estimates reasonably compatible with the observed data under the method used. It is not a range containing a known true value with certainty, and it does not assign a probability to the treatment being beneficial. For each primary recalculation, the interval includes zero, which corresponds to no risk difference. The intervals also extend to positive and negative values, so the data do not precisely distinguish the direction or size of the contrast.

Why are odds ratios also reported?

The registry reports logistic regression analyses using odds ratios. An odds ratio compares the odds of the outcome between groups, whereas a risk difference compares observed proportions by subtraction. These measures are on different scales, so their numerical values are not interchangeable. The record identifies the analyses as logistic regression and lists the four groups, but does not identify the specific estimand represented by each of the two reported odds ratios. It also does not report the model terms, covariates, or adjustment details. Interpretation should therefore stay with the method and estimates explicitly recorded.

What does the factorial structure add?

In general, a factorial design organizes assignment across more than one intervention component. In this trial, the components were digital support and NRT, with phone counseling common to every group. This structure can support questions about the components and their combination. However, the posted recalculations compare each non-reference arm separately with coaching only. They do not, by themselves, estimate a pooled effect for all participants assigned to NRT or all participants assigned to digital support, nor do they establish whether the two components interact. The registry record does not report enough detail to determine the sponsor’s factorial model or how the component hypotheses were tested.

Why can a non-significant result still be informative?

A p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be under the assumptions of a statistical test. It is not the probability that the null hypothesis is true, nor a measure of the importance of an effect. The unadjusted p-values for the primary pairwise recalculations are 0.767, 0.232, and 0.239. Together with the broad confidence intervals, they indicate that these comparisons do not give a precise estimate of the differences. They do not prove equivalence or show that the groups are identical.

How should the planning illustrations be understood?

The displayed planning illustrations use observed effects as inputs and are not a record of the trial’s original design calculations. In general, sample-size planning asks how many participants would be needed under specified assumptions to have a stated chance of detecting an effect of a chosen size at a chosen significance level. These projections are conditional on those assumptions and on the observed effect used as a starting point. They are not evidence that the completed trial had a particular probability of detecting its true effect.

For continuous secondary outcomes, the registry reports means and standard deviations, and the posted recalculations compare group means. A mean difference is the difference between the two group averages; its confidence interval reflects uncertainty in that estimate. Standard deviation describes participant-to-participant spread within a group, not the precision of the mean itself. The small groups contributing to some secondary measures and the spread in the measurements are relevant to how precisely those contrasts can be estimated. The registry record does not report a complete account of the analysis choices for these secondary outcomes.

11. Confidence Intervals and Precision

The primary recalculated confidence intervals are wide relative to their point estimates. For digital support alone, the risk-difference interval runs from -0.102 to 0.138. For NRT without digital support, it runs from -0.047 to 0.194. For the combined digital-and-NRT group, it runs from -0.049 to 0.195. Each interval includes zero and includes possible differences in both directions. This means the posted summaries do not tightly determine the size or direction of the group contrasts.

Precision is distinct from whether an estimate meets a conventional significance threshold. A point estimate gives the best single summary under the calculation, while the confidence interval indicates how much uncertainty surrounds it. A wide interval may include values that would be interpreted differently in practical terms. The record does not specify a threshold for a clinically important difference, so the intervals cannot be classified against such a threshold from the registry information alone.

The interval widths are consistent with the fact that the primary comparisons involve groups of 122, 126, 126, and 134 participants, along with outcome counts that are not large relative to the group sizes. In general, precision depends on the amount of information in the data and on the variability of the outcome. This is a general statistical explanation, not an additional trial result.

The sponsor’s reported odds-ratio intervals also include 1: 0.91 to 1.84 for the estimate of 1.30, and 0.73 to 1.47 for the estimate of 1.04. Because the registry does not map those two estimates to specific contrasts, they cannot resolve the pairwise interpretation. The overall message from the reported intervals is uncertainty about the size of differences, not proof of no difference.

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 illustrations are based on the observed effect and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each illustration, the effect to detect is set to the stated fraction of the observed effect. The displayed figures for these comparisons are participants per arm, not total participants across both arms. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation would require, under its assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column applies the same idea with a 90% chance. These are conditional planning probabilities, not probabilities that the trial result is correct. This is not observed power.

Rows that plan for 75% or 50% of the observed effect ask what the required group size would be if the effect of interest were smaller than the observed estimate. Smaller effects are harder to distinguish from random variation, so they generally require more participants. That pattern is apparent across the planning figures, including the very large requirements associated with small observed differences. These calculations are illustrations, not recommendations and not evidence that the trial should have enrolled a particular number. Their results depend on the stated assumptions and the effect size selected for planning.

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 = 0.410; treatment proportion p₁ = 0.429; average p̄ = 0.420.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6979 = 1.3678.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6978 = 0.5873.
4. n = (1.3678 + 0.5873)² / (0.0181)² = 11,636.9, rounded up to 11,637 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 <- 0.41044776119403                          # control proportion
p1 <- 0.428571428571429                          # 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(4974580)
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 = 11,637 (80% power), 15,579 (90% power)
 75% of observed effect: n per arm = 20,658 (80% power), 27,654 (90% power)
 50% of observed effect: n per arm = 46,408 (80% power), 62,127 (90% power)
power.prop.test: 11636.9 
Simulated power at n = 11,637 per arm: 0.795 (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 logistic regression, each listed for all four groups. One gives an odds ratio of 1.30 with a 95% confidence interval from 0.91 to 1.84 and p = 0.14. The other gives an odds ratio of 1.04 with a 95% confidence interval from 0.73 to 1.47 and p = 0.84. The record does not specify which comparison or factorial term each estimate represents, so the contrast cannot be identified from the entry alone.

The recalculated risk differences compare each non-reference arm with coaching only using posted group counts. They are simple, unadjusted contrasts, while the sponsor’s results are reported as logistic regression odds ratios. The measures differ, and the registry does not give enough model details to treat them as estimates of precisely the same quantity. The recalculations are therefore a descriptive companion to, not a replacement for, the sponsor’s analyses.

The record does not flag a discrepancy between the sponsor results and the recalculations. The sponsor’s own analysis remains the primary inferential result for the trial, while the recalculations help make the observed pairwise group contrasts explicit. Neither set of estimates should be read as establishing equivalence or a definitive absence of differences.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several research questions and multiple outcomes, with more than one intervention comparison and two sponsor-reported regression analyses. Considering multiple outcomes, contrasts, and hypotheses raises multiplicity: as the number of statistical tests grows, the chance of a seemingly unusual result arising by chance can also grow. In general, a prespecified testing hierarchy or other adjustment can help control this issue. The registry record does not report whether a multiplicity adjustment, hierarchical testing plan, or other strategy was specified or used.

Missing outcome data are addressed explicitly for the primary endpoint: participants missing the outcome were imputed as not abstinent. This rule defines how missing primary outcomes enter the reported result, but it does not reveal how many outcomes were missing, whether missingness differed among groups, or why participants did not provide outcome data. Those details are not reported in the registry record. The record also does not state whether sensitivity analyses examined alternative assumptions about missing outcomes.

The primary population is described as all participants fully enrolled at baseline. This is useful information about inclusion, but the entry does not provide a fuller account of analysis populations or protocol deviations. The registry record does not report whether an intention-to-treat label was applied, whether any participants were excluded after enrollment, or how adherence to assigned components was handled in analysis.

The trial’s detailed statistical analysis plan is not reported in the registry record. In particular, the record does not establish whether the final models included covariates, how the factorial structure was modeled, whether an interaction between digital support and NRT was assessed, or how the two sponsor-reported odds ratios correspond to the hypotheses. These gaps limit the ability to reconstruct the complete inferential strategy from the posted entry alone.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in each of the four groups, with serious-event risk groups of 134, 126, 126, and 122 participants. It also reports zero deaths in each group. These are the serious-event and death counts recorded in the adverse-event data.

Other adverse events were reported in the groups: 14 among 102 at risk in coaching only, 10 among 87 at risk in digital support, 33 among 96 at risk in coaching plus NRT, and 33 among 94 at risk in digital plus NRT. These are the registry’s counts of other affected participants and numbers at risk; they are not the serious-event counts. No serious-event terms are listed in the registry record.

Zero serious events recorded does not establish that the interventions are free of risk. The counts describe what was reported within this trial and its recorded follow-up, and the record does not provide further detail about event definitions, severity categories for other events, timing, or attribution. The non-serious counts should not be interpreted as proving that an intervention caused an event, nor do the zero serious-event counts rule out uncommon harms.

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

The posted results describe a randomized comparison of four support combinations, all against a shared background of phone counseling. For the primary endpoint, the observed abstinence counts differ across groups, but the unadjusted risk-difference confidence intervals include zero and extend in both directions. The estimates are therefore not precise enough to settle the size or direction of the group differences.

That statistical uncertainty is not the same as demonstrating that the groups are equal. A failure to establish a clear difference can arise when the true effects are small, when data are variable, or when estimates are imprecise; the posted record does not distinguish among these possibilities. Equivalence would require an appropriate design and prespecified bounds, which are not reported in the registry record.

The primary measure captures self-reported vaping abstinence over the 7 days before the 3-month survey. It does not show continuous abstinence throughout follow-up, and it is not a direct measure of long-term cessation. The missing-data rule treats missing primary outcomes as not abstinent, but details about missingness and sensitivity analyses are not reported. Secondary outcomes address other aspects of vaping and dependence but are not interchangeable with the primary endpoint.

The trial’s results apply to the enrolled population and the interventions as described in the registry. They do not establish which component or combination is best in settings or populations not studied. The registry record does not report the detailed factorial model, the mapping of the sponsor’s two odds ratios to specific comparisons, or a complete plan for multiple testing. These limits matter when drawing conclusions beyond the observed group summaries and the sponsor’s reported analyses.

18. Why This Trial Matters Statistically

Statistically, this trial illustrates how factorial randomization can organize questions about multiple intervention components while keeping a shared background treatment constant. Here, all groups received phone counseling, and assignment varied with respect to digital support and NRT. That arrangement makes the component questions meaningful, but the interpretation depends on how the factorial structure is analyzed. The registry describes the design but does not report enough analysis detail to reconstruct all component-level tests.

The endpoint also shows why outcome definitions matter. A 7-day point-prevalence measure is a specific, interpretable snapshot, but it does not represent continuous abstinence or every aspect of vaping behavior. Reporting the assessment window and the missing-data rule allows readers to understand what the primary counts mean and what they leave out.

Another statistical lesson is the distinction between a point estimate and its precision. The recalculated primary contrasts have confidence intervals that include zero and cover both positive and negative differences. The observed estimates alone might invite a ranking of groups, but the uncertainty does not support a firm ranking. Confidence intervals help make that uncertainty visible, while p-values alone would not describe its range.

Finally, sample-size planning illustrations based on observed effects can be informative for future planning, but they do not tell readers whether the completed trial was adequately designed. The original design assumptions are not reported, and planning figures depend on the chosen effect and calculation assumptions. Separating planning projections from observed trial evidence prevents an inappropriate claim about what the trial was powered to find.

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 leaves several limits on interpretation. It does not report the original sample-size justification, detailed randomization methods, masking details, or a complete statistical analysis plan. Although the study is described as factorial, the record does not identify the final model’s treatment of the two components or whether their interaction was assessed. The two reported logistic regression odds ratios are not mapped to specific contrasts.

The primary outcome is self-reported point-prevalence abstinence at one follow-up time. The record does not report verification of self-reports, the extent or distribution of missing outcomes, or sensitivity analyses for the rule that missing outcomes were counted as not abstinent. Consequently, the effect of missing-data assumptions on the estimates cannot be assessed from the entry.

There are several secondary outcomes and comparisons, but the registry record does not report a multiplicity strategy or identify which secondary analyses were intended to be confirmatory. Some secondary summaries include fewer participants than the primary outcome, limiting their precision. A Penn State dependence measure is named among secondary outcomes, but a corresponding posted result is not included in the secondary entries.

The registry descriptions establish that phone counseling was common to all groups, but they do not provide detailed information about intervention fidelity, actual engagement with digital materials, NRT use, or adherence. These factors could help explain differences between assignment and exposure, but their analysis is not reported in the registry record. The adverse-event entry reports counts, but does not give further information on event timing, attribution, or definitions. These limitations constrain how much can be inferred beyond the recorded outcomes and comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Research and Innovation to Stop E-cigarette/Vaping in Young Adults — NCT04974580.
• Registry record last updated 2024-07-29; status last verified 2024-07.
• Results first posted 2024-07-29.
• 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

NCT04974580, “Research and Innovation to Stop E-cigarette/Vaping in Young Adults,” is a completed, randomized, single-masked, phase 4 factorial trial sponsored by Ohio State University. Enrollment was 508. All groups received phone counseling, with randomized additions of digital cessation support, NRT, both, or neither.

The primary endpoint was self-reported 7-day vaping abstinence 3 months after the first coaching call. Missing primary outcomes were imputed as not abstinent. The observed counts varied across groups, while the unadjusted pairwise risk-difference intervals included zero and remained broad. The registry also reports two logistic regression odds ratios, but does not map them to specific contrasts.

The entry lists secondary outcomes and adverse-event counts. Details on the original sample-size rationale, full statistical plan, multiplicity handling, and several analysis choices are not reported in the registry record.