Effects of E-cigarette Flavors on Youth TCORS 2.0: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of E-cigarette Flavors on Youth TCORS 2.0 (NCT03634839), a randomized phase 1 study. The primary outcome is Liking: Difference Score in Liking/Wanting of Each E-cigarette Condition.

2. Clinical Question

3. Trial Design

The registry describes NCT03634839, Effects of E-cigarette Flavors on Youth TCORS 2.0, as a phase 1, randomized, triple-masked crossover study sponsored by Yale University. Its status is completed. The listed enrollment is 42. The registry dates the study start to 2022-11-07 and primary completion to 2023-06-16.

A crossover design means participants receive more than one study condition, allowing their responses under different conditions to be compared. In this study, the arm descriptions identify sweet non-menthol nicotine and sweet menthol nicotine conditions, both at 36mg/ml nicotine. The registry records two puff bouts and measures liking after each condition. The order of condition administration, any washout procedure, and how these aspects were handled in the analysis are not reported in the registry record.

Triple masking indicates that the registry classified the study as masked at three levels, but it does not name the masked parties or explain how masking was maintained. Those details are not reported in the registry record. The record lists Flavoring Agents and Nicotine as drug interventions. The specific procedures for administration, puffing, and assessment beyond the posted outcome description are not reported in the registry record.

The result assessed is a continuous liking score. The registry lists four outcome measures and four analyses, but the details of the other outcomes are not included in the posted results described for the primary endpoint. The number of participants contributing to each primary endpoint condition is 40 in the posted outcome data; those outcome counts need not be interpreted as the enrollment figure. Reasons for any difference between enrollment and endpoint counts are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: A total of 40 participants completed the study. Specifically, 49 out of 84 participants were randomized, but 7 did not show up and 2 withdrew. Of the 35 who were not randomized, 18 did not meet inclusion criteria and 17 did not show up.

First Intervention (2 Hours)

Reasons for not completing this period:

30 Minutes Break

Second Intervention (2 Hours)

Analysis population for the primary outcome, as defined in the registry: After each of the two puff bouts, we evaluated participants' reference for the overall experience of the e-cigarette using the LHS, which is a bipolar category ratio scale that spans from -100 (most disliked) to 100 (most liked), with 'neither liked nor disliked' positioned as the midpoint. The scale labels were places along the scale based on their semantic magnitude.

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 Liking: Difference Score in Liking/Wanting of Each E-cigarette Condition, measured over Following administration of e-cigarette condition 1 (+10 minutes), following administration of e-cigarette condition 2 (+40).

The primary endpoint is titled Difference Score in Liking/Wanting of Each E-cigarette Condition. It uses the Labeled Hedonic Scale, a bipolar category-ratio scale that places the most disliked sensation imaginable at -100 and the most liked sensation imaginable at 100, with neutral at 0. Higher values indicate greater liking. The listed scale anchors also include intermediate verbal categories, from dislike slightly to like extremely.

Participants rated the overall experience after each of the two puff bouts. The registry gives assessment times as following condition 1 (+10 minutes) and following condition 2 (+40). The posted outcome values are least-squares means, with standard errors as the dispersion measure. The endpoint is useful for comparing participants' immediate subjective ratings across the two flavor conditions. It measures reported liking, not a clinical diagnosis, long-term behavior, or a direct measure of future nicotine use.

The posted values are 1.268 for sweet non-menthol nicotine and -3.916 for sweet menthol nicotine. The registry analysis reports a mean difference in final values of -5.184 for the menthol condition relative to the non-menthol condition. These scores describe the direction and size of the observed rating contrast on the scale; their interpretation should remain tied to this endpoint and its assessment context.

7. Results Posted in the Registry

• Sweet Menthol, Nicotine 36mg/ml: mean -3.92 versus 1.27 on control; difference -5.18 (95% CI -13.94 to 3.57), standardized effect d = -0.26; z-test p = 0.246.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is continuous: it is a numerical rating on the Labeled Hedonic Scale. For a continuous measure, a mean summarizes the central value of participants' scores, while a standard error describes uncertainty around an estimated mean. The registry identifies the posted arm values as least-squares means and lists standard errors of 3.158 for both conditions. The registry record does not describe the model used to obtain those least-squares means.

What does the mean difference represent?

The mean difference compares the posted final liking values for the two conditions. The registry's reported estimate is -5.184 for sweet menthol relative to sweet non-menthol. A negative contrast means the menthol condition's posted mean is lower under that subtraction direction. Since higher scale values indicate greater liking, the sign describes the direction of the rating contrast; it does not by itself establish whether the difference is important in practice.

The reported registry analysis is a two-sided t-test of the mean difference in final values. A two-sided test considers departures in either direction rather than only a prespecified increase or decrease. The registry lists the analysis type as superiority and reports p = 0.053, but does not post a confidence interval or further detail on the test implementation. The registry record does not report whether the test accounted for the crossover structure or what model terms, if any, were used.

What is the unadjusted recalculation?

The recalculation uses the posted arm means and standard errors to produce an approximate, unadjusted comparison. It reports a mean difference of -5.184, a 95% confidence interval from -13.94 to 3.569, and p = 0.246. The calculation uses an approximate pooled standard deviation, as indicated in the calculation description. It is not the sponsor's analysis and does not reproduce any unreported model specification.

General statistical context: in a parallel-group comparison, an independent-groups calculation treats the groups' observations as independent. In a crossover study, the same participant contributes measurements under multiple conditions, so the within-participant relationship can affect uncertainty in the contrast. Retaining that relationship generally requires paired data or an analysis that models it. The posted summary statistics do not provide that covariance, so the recalculated interval and p-value should be regarded as approximate rather than as a design-faithful reanalysis.

Why do the confidence interval and test matter together?

A confidence interval gives a range of effect values compatible with the estimate under the calculation's assumptions. The recalculated interval crosses zero, which represents no mean difference, and extends to both negative and positive values. It therefore does not isolate a single direction of contrast. The interval's breadth also conveys that the estimate is not highly precise under this recalculation. The registry's own estimate has no posted interval, limiting direct assessment of its precision.

A p-value summarizes how unusual a test statistic would be under a specified null model and assumptions. It is not an effect size and does not describe the probability that the null hypothesis is true. For this reason, the registry p-value and the recalculated p-value should not be treated as interchangeable or judged without their analytic bases. Their difference makes the lack of detail about the registry's analysis particularly relevant.

What does masking and randomization contribute?

Random allocation can help reduce systematic differences in the order or assignment of conditions, while masking can reduce influences on ratings or their assessment. Those are general design considerations, not proof that bias was eliminated. The registry identifies the design as randomized and triple-masked but does not report the allocation sequence, the masked parties, or checks on masking. Because the study is crossover, condition order and carryover may also matter; details of their handling are not reported in the registry record.

Overall, the registry's own two-sided t-test is the primary reported inferential result. The unadjusted calculation adds a transparent summary-statistic comparison, but its approximations and the missing crossover covariance prevent it from resolving the registry analysis. A fuller statistical account, including model specification and handling of repeated measurements, is not reported in the registry record.

10. Confidence Intervals and Precision

The registry reports a mean difference of -5.184 but does not post a confidence interval for its own analysis. As a result, the precision of that specific registry estimate cannot be read directly from a reported interval. The posted standard errors for the two least-squares means are each 3.158, but they do not alone supply the covariance needed to assess a within-participant contrast in a crossover study.

The unadjusted recalculation gives a 95% confidence interval from -13.94 to 3.569 around the mean difference. A confidence interval describes a range of values compatible with the data and calculation assumptions; it is not a guarantee that the true value lies within that particular interval. Because this interval includes zero, the recalculation does not distinguish the observed contrast from no mean difference at the confidence level used. It also includes contrasts in the opposite direction from the point estimate.

The interval is based on summary statistics and an approximate pooled standard deviation, rather than a reported crossover model that incorporates within-participant covariance. Its precision should therefore be interpreted cautiously. The width indicates uncertainty in this approximate estimate, while the absence of a registry confidence interval leaves the precision of the sponsor's own analysis less fully documented. The registry record does not report additional interval estimates for the primary comparison.

11. 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 figures are planning illustrations based on the observed effect, not a report of the trial's original design calculation. They are stated as participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario considers detecting a stated fraction of the observed effect. The registry record's original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned participants per arm under which the calculation would have an 80% chance of detecting the specified effect if the assumptions and effect were correct. The 90% power column expresses the corresponding planning target for a 90% chance under those assumptions. These are design-planning quantities, not guarantees about what a future study will find. The displayed scenarios include planning for 100%, 75%, and 50% of the observed effect.

As the target effect becomes smaller, it is harder to distinguish it from ordinary sampling variation, so more participants are needed for the same planned power. The figures are based on an observed effect from this study and should not be read as evidence that the observed effect is stable or that the assumed effect will recur. This is not observed power; it is a planning illustration under the listed assumptions.

Because the trial is crossover, these calculations' equal-allocation, two-arm framing does not by itself describe how a future crossover trial should be designed. The posted planning assumptions do not specify a within-participant correlation or another crossover-specific variance model. The figures are best read as illustrative participant-per-arm requirements for the stated simplified assumptions.

12. 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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -5.184; pooled standard deviation σ = 19.973.
2. n = 2 × (1.96 + 0.842)² × 19.973² / -5.184² = 233.0, rounded up to 234 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
delta <- -5.184                      # observed difference in means
sigma <- 19.9729457016235                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3634839)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 234 (80% power), 312 (90% power)
 75% of observed effect: n per arm = 415 (80% power), 555 (90% power)
 50% of observed effect: n per arm = 933 (80% power), 1,248 (90% power)
power.t.test: 234 
Simulated power at n = 234 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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.

13. Analyses Reported by the Sponsor

The registry analysis reports a two-sided t-test of the mean difference in final values: -5.184, with p = 0.053. It does not post a confidence interval. The unadjusted recalculation also gives a mean difference of -5.184, but its approximate confidence interval is -13.94 to 3.569 and its p-value is 0.246.

The matching point estimates do not mean the analyses are identical. The recalculation uses posted summary statistics, including an approximate pooled standard deviation, and does not preserve the within-participant covariance that may matter for a crossover study. The registry record does not provide enough detail to determine precisely why its p-value differs. The registry's own analysis remains the primary reported analysis; the recalculation is supplementary context, not a correction or substitute.

The registry does not post the sponsor analysis's interval, model details, or information about how repeated condition measurements were handled. Those omissions limit independent assessment of the sponsor result. The reported p-value should be interpreted as a test result under the sponsor analysis, not as a measure of the size, importance, or probability of the observed contrast.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures and four analyses, while the posted secondary outcome count is 0. The primary outcome is the liking difference score. The record does not explain how the four analyses correspond to outcomes or comparisons, whether each was prespecified as primary or secondary, or whether any adjustment for multiple testing was applied. A multiplicity adjustment or its absence is not reported in the registry record.

Multiplicity matters when several outcomes or contrasts are tested: the more tests considered together, the greater the chance of at least one apparently unusual result under a set of null effects. That is general statistical context, not a claim that an adjustment was required or omitted in this trial. Without a reported testing hierarchy or adjustment strategy, the p-value should be read as the result for the posted comparison and not as a fully documented family-wise conclusion.

The registry does not report how missing endpoint observations were handled, whether participants with incomplete condition ratings were excluded, or whether any imputation was used. The posted primary outcome counts are 40 for each condition, while listed enrollment is 42. The reason for this difference is not reported in the registry record, and the outcome counts alone do not explain missingness or the analysis population.

The analysis population, including whether the analysis followed an intention-to-treat principle or another defined set, is not reported in the registry record. The registry also does not describe protocol deviations, exclusions, or how participants who did not complete both conditions were treated. These details matter because excluding or retaining particular observations can affect the estimate and its uncertainty.

Finally, the registry identifies a crossover design but does not report the analysis model, the handling of condition order or carryover, or the participant-level pairing used in the sponsor test. These are important elements for interpreting repeated measurements. Their absence does not establish that they were mishandled; it means that the posted record does not allow readers to evaluate the approach in detail.

15. 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.

Most frequent non-serious adverse event terms

The posted serious adverse event figures list 0 serious adverse events and 0 deaths in each condition. The number at risk is 40 for sweet non-menthol nicotine and 42 for sweet menthol nicotine. The registry also lists 0 other adverse events for the non-menthol condition and 2 for the menthol condition. These are adverse-event counts as posted, not an estimate of comparative risk.

The record does not provide serious adverse event terms, since no serious terms are listed. It does not describe event timing, severity beyond the serious versus other categories, relatedness assessment, or how adverse events were collected. The differing at-risk counts are recorded as given; the registry does not explain them. These data should be read as the reported safety observations for this study and not as evidence that events cannot occur outside the recorded observations.

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

The main posted finding is a difference in immediate liking ratings between two sweet nicotine e-cigarette conditions. The registry estimate is -5.184 for sweet menthol relative to sweet non-menthol. The point estimates put the menthol condition lower on the scale, where higher values indicate greater liking. The registry's two-sided test reports p = 0.053, while the summary-statistic recalculation gives p = 0.246 and a confidence interval that crosses zero.

These results do not provide a clear, precise estimate of the underlying contrast. The registry analysis lacks a posted confidence interval, and the recalculated interval is approximate and incorporates assumptions that may not fully represent a crossover comparison. The record also does not explain the difference between the registry and recalculated p-values. Those limitations argue for cautious interpretation of the apparent direction and magnitude.

The endpoint reflects participants' ratings after each puff bout. It does not measure long-term preference, changes in nicotine use, dependence over time, or clinical outcomes. The study's stated aim includes appeal and abuse potential, but the posted primary result addresses liking ratings; it cannot alone answer every aspect of that broader aim.

The comparison is between sweet watermelon with nicotine and sweet watermelon-menthol with nicotine, both listed at 36mg/ml. It does not isolate all components of e-cigarette appeal or compare against a nicotine-free condition in the posted arms. The registry record does not report enough detail about study context or participant characteristics to generalize the rating contrast beyond the recorded study population and conditions.

Accordingly, the result is best understood as a study-specific comparison of subjective scores, with uncertainty and analytic limitations. It neither establishes a general effect of menthol flavor nor supports conclusions about later behavior or health outcomes.

17. Why This Trial Matters Statistically

This trial illustrates why the design and analysis need to be interpreted together. A crossover study observes participants under multiple conditions, which can make within-person comparisons informative. At the same time, such a design requires attention to the dependence between each participant's measurements. The registry labels this study as crossover, but the posted analysis details do not explain how that dependence was handled.

The posted score difference is accompanied by a registry p-value and a separate recalculation with a confidence interval. The point estimates match, yet the p-values differ. This makes a useful statistical distinction visible: an estimate, its uncertainty, and the method used to quantify uncertainty are related but not interchangeable. Without a posted registry interval or model details, readers cannot fully assess the sponsor analysis's precision from the registry record alone.

The outcome also demonstrates the importance of matching conclusions to measurement. A liking scale can quantify immediate subjective response, but it does not automatically measure sustained use or abuse potential. Statistical interpretation should stay close to what the endpoint records, even when the broader study rationale concerns additional behavioral questions.

Finally, planning illustrations based on an observed effect can show how sample-size needs change with the target effect, but they are not a substitute for the trial's original design rationale. The record does not report that rationale. Together, these features make the trial a useful example of reading registry results with attention to estimand, design, precision, multiplicity, and what remains undocumented.

18. 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.

Several limitations specific to this record constrain interpretation. Although the study is identified as randomized, triple-masked, and crossover, the registry does not report condition sequence, allocation implementation, masked parties, or procedures for maintaining masking. It also does not report whether or how condition order and possible carryover were addressed. These details are important for understanding comparisons where participants experience both conditions.

The primary outcome data give least-squares means and standard errors, but the model that produced them is not described. The registry analysis reports a two-sided t-test and a point estimate but no confidence interval. A summary-statistic recalculation gives an approximate interval and a different p-value, and it cannot incorporate the unreported within-participant covariance. The record does not explain the difference between these analyses.

The posted outcome counts do not match the listed enrollment figure, and the reasons are not reported in the registry record. Missing-data methods, analysis population definitions, participant exclusions, and completion of both conditions are likewise not described. This limits assessment of whether the posted comparison represents all enrolled participants or a selected set.

Multiplicity handling is not reported, despite the record listing multiple outcome measures and analyses. The relation between the listed analyses and any testing hierarchy is unclear. Also not reported are detailed eligibility criteria, participant ages, scale administration procedures beyond the posted description, and the study's original sample-size rationale.

Finally, the endpoint is a short-term rating after puff bouts. The registry record does not post secondary results that would allow the primary liking score to be placed alongside other measures of appeal or abuse potential. Generalization beyond these two sweet nicotine conditions and the recorded study population is therefore limited.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effects of E-cigarette Flavors on Youth TCORS 2.0 — NCT03634839.
• Registry record last updated 2024-08-09; status last verified 2024-07.
• Results first posted 2024-08-09.
• 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.

22. Record Summary

NCT03634839 is a completed, phase 1 randomized, triple-masked crossover study sponsored by Yale University. The registry lists enrollment of 42 and compares sweet non-menthol nicotine 36mg/ml with sweet menthol nicotine 36mg/ml in a study of e-cigarette flavor and youth.

The primary endpoint is a Labeled Hedonic Scale liking score assessed after each condition. The registry reports a mean difference of -5.184 and a two-sided t-test p-value of 0.053. An unadjusted summary-statistic recalculation gives a 95% confidence interval from -13.94 to 3.569 and p = 0.246. The registry does not post a confidence interval for its own analysis or enough detail to reconcile the differing p-values.

The posted results describe immediate ratings, not longer-term use or clinical outcomes. Important details about the crossover analysis, missing data, multiplicity, and the original sample-size rationale are not reported in the registry record.