Evaluation of the Efficacy of 3M Dry Mouth Moisturizing Spray: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Efficacy of 3M Dry Mouth Moisturizing Spray (NCT04186806), a randomized na study. The primary outcome is 10 cm Mouth Dryness Visual Analog Score.

2. Clinical Question

3. Trial Design

The registry describes a randomized, single-masked crossover trial of 3M Dry Mouth Moisturizing Spray and Biotene Moisturizing Mouth Spray. Both products are described as dry mouth agents, and Biotene is an active control. Enrollment was 40. The study is listed as completed, with a start date of 2019-11-02 and a primary completion date of 2019-12-13. The phase is listed as NA.

In a crossover design, participants receive more than one treatment in a sequence, so outcomes may be compared within participants as well as between treatment periods. The registry lists sequences of 3M spray followed by Biotene and Biotene followed by 3M spray. This is consistent with the crossover designation. Details such as treatment duration, washout arrangements, sequence allocation proportions, and handling of period or carryover effects are not reported in the registry record.

Single masking means the record identifies the study as masked at one level; which people were masked is not reported in the registry record. The registry does not state the randomization method or allocation concealment approach. The sponsor is Solventum US LLC. The registry describes the purpose as evaluating and validating the experimental mouth spray's performance when used by people with mild to severe dry mouth symptoms.

The primary outcome is a continuous score assessed 15 minutes after dosing. A sponsor-reported mixed models analysis is also listed for final values. The registry record does not explain whether that model included treatment sequence, period, or other terms. The posted results include secondary outcomes at additional time points, but do not provide a complete account of the planned analysis strategy.

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.

Period 1: 7 Days

Reasons for not completing this period:

Washout Period: at Least 2 Days

Period 2: 7 Days

Analysis population for the primary outcome, as defined in the registry: Intent to treat (ITT) with Group Means Imputation

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 10 cm Mouth Dryness Visual Analog Score, measured over 15 minutes post dose.

The primary endpoint is the mouth dryness visual analog score, measured in centimeters on a 10 cm scale, at 15 minutes after dosing. The scale is described as ranging from 0, representing normal, to 10, representing the worst imaginable dry mouth symptoms. A visual analog scale turns a participant's subjective experience into a continuous measure, allowing the recorded symptom level to vary across the scale rather than forcing it into a small set of categories.

The registry specifies a mean measure with standard deviation and says the primary endpoint is the paired difference between the experimental and active control products. Pairing is relevant to a crossover trial because the same participant can contribute observations under both treatments. A within-participant comparison can account for stable differences between participants, although the registry does not report the precise paired-analysis formula or its covariance assumptions.

The endpoint is used to compare reported symptom severity at a specified post-dose time. The direction of the scale gives the score an interpretable meaning: lower scores are closer to normal, while higher scores are closer to the worst imaginable symptoms. The endpoint represents a particular measurement at 15 minutes, not every aspect of dry mouth or symptom experience over time. The registry record does not report a threshold for a clinically important difference, so the clinical meaning of a difference of any particular size cannot be determined from this record alone.

7. Results Posted in the Registry

• Biotene Moisturizing Mouth Spray: mean 4.60 versus 4.51 on control; difference 0.09 (95% CI -0.97 to 1.15), standardized effect d = 0.04; z-test p = 0.868.

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.

10 cm Mean Mouth Dryness Visual Analog Score

• 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:
  • Biotene Moisturizing Mouth Spray: mean 5.68 versus 5.14 on control; difference 0.54 (95% CI -0.33 to 1.41), standardized effect d = 0.27; z-test p = 0.226.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biotene Moisturizing Mouth Spray and the control. The interval gives the range of effects that remain compatible with the data.

10 cm Mouth Dryness Visual Analog Score

• 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 errors.
• Result:
  • Biotene Moisturizing Mouth Spray: mean -1.67 versus -2.32 on control; difference 0.66 (95% CI -0.27 to 1.59), standardized effect d = 0.31; z-test p = 0.166.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biotene Moisturizing Mouth Spray and the control. The interval gives the range of effects that remain compatible with the data.

10 cm Mean Mouth Dryness Visual Analog Scale

• 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:
  • Biotene Moisturizing Mouth Spray: mean 4.75 versus 4.51 on control; difference 0.24 (95% CI -0.76 to 1.24), standardized effect d = 0.10; z-test p = 0.639.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biotene Moisturizing Mouth Spray and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the dryness assessments beyond the primary 15-minute endpoint. Across the posted measures, estimated differences vary in size and direction, and the intervals include zero. The overall pattern does not provide a clearly separated set of estimates that would overturn or sharpen the interpretation of the primary result. These additional measures are relevant as context because they describe symptom scores at other times, but they are not a substitute for the prespecified primary question.

Several outcome titles are repeated or very similar, and the record lists 41 posted secondary outcomes. The titles include mean and non-mean visual analog scores and measurements at different times. The registry does not describe how these measures relate to one another analytically or identify which, if any, were selected as key confirmatory secondary endpoints. This limits the ability to treat each result as a separate, independent piece of evidence.

Secondary p-values are unadjusted, and no strategy for multiplicity is reported in the registry record. When many outcomes or time points are examined, some estimates may appear more compelling by chance alone. Without a declared hierarchy or adjustment plan, individual secondary findings should carry less weight than the primary endpoint and should be interpreted as exploratory. Their main contribution is to show whether the broad pattern of scores is consistent with the primary comparison, not to establish a separate conclusion for every listed measure.

The registry includes 42 outcome measures overall and one analysis for the primary comparison. The presence of numerous outcomes does not mean every possible analysis was performed, but the record does not describe the full set of planned comparisons. Accordingly, the secondary results are best read alongside their uncertainty and the missing multiplicity details rather than as a collection of standalone tests.

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

• 10 cm Mean Mouth Dryness Visual Analog Score
• 10 cm Mouth Dryness Visual Analog Score
• 10 cm Mean Mouth Dryness Visual Analog Score
• 10 cm Mean Mouth Dryness Visual Analog Scale
• 10 cm Mean Mouth Dryness Visual Analog Scale
• 10 cm Mean Mouth Dryness Visual Analog Scale
• 10 cm Mouth Dryness Visual Analog Scale
• 10 cm Mouth Dryness Visual Analog Scale

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help interpret the results without treating any one number as a complete answer. The primary outcome is continuous: it records a score on a visual analog scale rather than a yes-or-no event. For a continuous outcome, a mean describes the central level of the scores, while a standard deviation describes variation among observations. These answer different questions. A mean comparison describes the estimated difference in average score; the standard deviation describes how dispersed scores are.

What does a paired comparison mean?

The primary endpoint is described as a paired difference. In a crossover study, participants can contribute measurements under both products, and the difference within a participant can be analyzed. This approach can reduce the influence of stable person-to-person differences because each participant serves as their own comparison. The analysis still needs to account appropriately for the trial's structure. The registry record does not report the full paired-analysis method, the handling of period effects, or whether possible carryover was assessed. Those details matter to how confidently the result can be interpreted as a treatment comparison.

The recalculated mean difference uses the posted summary statistics and is described as unadjusted. It is not the same thing as the sponsor's mixed-model estimate. A summary-statistic recalculation cannot reconstruct unreported participant-level pairing or all model terms. The recalculated result is therefore a useful descriptive comparison, while the sponsor's stated analysis remains the sponsor's analysis of record. Since the registry does not report a p-value for the mixed-model result, that value should not be inferred from its confidence interval.

How should a confidence interval be read?

A confidence interval gives a range of estimates compatible with the data and the statistical method used, under repeated-sampling interpretations. It conveys uncertainty more directly than a single point estimate. A narrow interval indicates greater precision than a wide interval on the same scale. When an interval includes zero for a difference, the data are compatible with no difference as well as with differences in either direction represented by the interval. That does not prove the treatments are identical. The primary recalculated interval extends from -0.972 to 1.152, and the sponsor-reported interval extends from -1.260 to 0.575; both are wide enough to encompass values on either side of zero.

A p-value summarizes the compatibility of data with a specified null model, given the analysis assumptions. The primary recalculated p-value is unadjusted. It is not an effect size, does not express the probability that the null hypothesis is true, and does not tell whether a difference is important to participants. Interpretation should consider the estimate, its confidence interval, the outcome's scale, and the design together.

What does the crossover structure add?

Randomization can help balance factors affecting outcomes across treatment assignment, while crossover comparisons can use within-participant information. In a crossover, the results can also depend on time, treatment order, and whether effects from an earlier period persist. The registry identifies randomization and a crossover model, but does not report the procedures or model terms used to address these issues. The sponsor's mixed models analysis may have accounted for features of the design, but the registry record does not give enough detail to specify which ones.

The record lists intent to treat with Group Means Imputation for the primary population. Intent-to-treat analysis generally aims to retain participants in the groups to which they were assigned. Group means imputation is a missing-data approach that substitutes a group mean for missing values, as described by the record. The number and timing of missing observations, the exact imputation procedure, and any sensitivity analyses are not reported in the registry record. Imputation can affect uncertainty and can rely on assumptions about missing observations; the record does not provide enough information to assess those assumptions.

Why do secondary outcomes need caution?

Multiple outcomes and time points create multiple opportunities to observe estimates that appear noteworthy by chance. A multiplicity adjustment is one way to address the increased false-positive risk that can arise when many hypotheses are tested. The registry lists 42 outcome measures and 41 posted secondary outcomes, with repeated or similar outcome titles among the listed measures. It reports one analysis for the primary result. A plan for controlling multiplicity across outcomes or time points is not reported in the registry record. Consequently, unadjusted secondary p-values are best treated as exploratory rather than as independent confirmation of the primary result.

The primary result and the secondary results describe measurements at particular times. They do not establish a general response across all people, times, or aspects of dry mouth. The estimates and intervals describe the precision of the posted comparisons, while incomplete reporting of model details, missingness, and multiplicity limits how far statistical conclusions can be extended.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate a treatment difference. The primary unadjusted recalculation estimates a mean difference of 0.09 cm, with a 95% confidence interval from -0.972 to 1.152. The interval spans zero and includes estimates favoring either direction under the comparison's sign convention. Its width means that the observed trial does not locate the difference narrowly. The p-value of 0.868 is consistent with the interval's failure to isolate a difference from zero, but the interval is more useful for seeing the range of estimates that remains compatible with the data.

The sponsor-reported mixed-model estimate is -0.343, with a 95% confidence interval from -1.260 to 0.575. This interval also includes zero. The record does not give the p-value for this model result, nor does it give sufficient coding and model detail to align its estimate directly with the unadjusted recalculation. The distinct estimates and intervals should therefore be described as results of different analyses, not blended into one estimate.

Precision is affected by the amount and variability of the observed data, along with the analysis method and design. The primary arm standard deviations are 2.228 and 2.604, and there were 40 participants in each posted arm summary. Because the endpoint is described as paired, the relationship between each participant's measurements is relevant; that correlation is not reported in the registry record. The posted arm summaries alone do not reveal it.

A confidence interval is not a range guaranteed to contain the true effect, nor does it indicate which values are clinically important. A clinically important threshold for the score difference is not reported in the registry record. The intervals can therefore be used to discuss statistical uncertainty, but they cannot determine whether any included difference would matter in practice.

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 express required sample sizes as participants per arm, not as total events. They are not the number enrolled or an estimate of how many participants the trial actually needed under its original protocol. For the primary comparison, the illustrations are based on 100%, 75%, and 50% of the observed effect. At 100% of the observed effect, the estimate is 11,381 participants per arm for 80% power and 15,236 participants per arm for 90% power. At 75%, it is 20,233 participants per arm for 80% power and 27,086 participants per arm for 90% power. At 50%, it is 45,523 participants per arm for 80% power and 60,943 participants per arm for 90% power.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

In plain terms, 80% power is the planning probability of detecting the assumed effect at the stated significance level if that effect is truly present and the assumptions hold. The 90% column uses a higher target probability of detection. Smaller assumed effects require more participants because they are harder to distinguish from random variation. These are planning illustrations based on the observed estimate, not observed power and not a retrospective assessment of whether the completed trial succeeded.

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

Worked calculation for this trial

1. Observed difference Δ = 0.090; pooled standard deviation σ = 2.423.
2. n = 2 × (1.96 + 0.842)² × 2.423² / 0.090² = 11,380.7, rounded up to 11,381 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 <- 0.0899999999999999                      # observed difference in means
sigma <- 2.42330353030734                     # 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(4186806)
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 = 11,381 (80% power), 15,236 (90% power)
 75% of observed effect: n per arm = 20,233 (80% power), 27,086 (90% power)
 50% of observed effect: n per arm = 45,523 (80% power), 60,943 (90% power)
power.t.test: 11381.6 
Simulated power at n = 11,381 per arm: 0.802 (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.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's own primary analysis as a mixed models analysis of final values. It is labeled non-inferiority and gives a mean difference of -0.343 with a 95% confidence interval from -1.260 to 0.575. The registry record does not report a p-value for this analysis. It also does not report the non-inferiority margin, the direction in which the model defines the difference, or enough model detail to reconstruct the result.

The recalculated comparison is an unadjusted calculation from posted summary statistics: the mean difference is 0.09 cm for Biotene relative to 3M, with a 95% confidence interval from -0.972 to 1.152 and an unadjusted p-value of 0.868. This calculation is not a substitute for the mixed model. In particular, it does not reproduce the paired participant-level data or any adjustments used in the sponsor's model. The estimates also use different presentations of the comparison, and the registry does not state enough about sign coding to explain their direction side by side.

The sponsor's own analysis takes precedence over the simple recalculation as the trial's reported analysis. However, a non-inferiority label alone is not sufficient to assess a non-inferiority conclusion: the margin and its rationale are essential, and they are not reported in the registry record. The posted information therefore permits a description of the sponsor's estimate and interval but not an independent evaluation of the non-inferiority criterion.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 42 outcome measures, including 41 posted secondary outcomes, and reports one analysis for the primary comparison. A multiplicity plan is not reported in the registry record. This matters because examining several outcomes or time points can increase the chance that at least one result appears unusual even when there is no underlying difference. Methods such as a prespecified testing hierarchy or an adjustment to significance thresholds can address that issue, but the record does not say whether such methods were used. The secondary p-values are unadjusted, so they should not be treated as confirmatory evidence on their own.

The primary analysis population is described as intent to treat with Group Means Imputation. Intent to treat generally seeks to preserve randomized assignment in analysis. Group means imputation indicates that missing observations were handled using group means, but the record does not specify the exact implementation, the groups used for imputation, or the number of values imputed. The amount and pattern of missing data, reasons for missingness, and sensitivity analyses are not reported in the registry record. These details are important for judging whether the imputation method could have influenced the result.

The record identifies a sponsor-reported mixed models analysis and a crossover design, but does not give its full model specification. Treatment sequence, period, carryover, and other model terms are not reported. Nor is the original sample-size calculation or its assumptions reported. The planning illustrations are separate from that original design rationale and should not be interpreted as evidence of what the trial was designed to detect.

These omissions do not establish that a particular method was or was not used; they limit what can be verified from the registry record. The primary estimate and its uncertainty can still be described, while firm interpretation of confirmatory secondary findings, missing-data sensitivity, and the non-inferiority analysis requires information not reported in the registry record.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: skin ulceration (2.5%).

The adverse event record lists serious adverse events affecting 1 of 40 participants in the 3M spray group and 0 of 39 in the Biotene group. Deaths are listed as 0 for each group. Other adverse events affected 7 of 40 participants in the 3M spray group and 7 of 39 in the Biotene group.

The registry also lists Skin Ulceration as a top serious term at 2.5%. The record does not provide enough detail to determine from this listing how the term relates to the serious event count or to attribute an event to a product. The adverse event figures describe counts recorded for the groups; they do not by themselves establish causation or compare risk with precision. Since this was a crossover study, participants may have received both products, but the registry's adverse-event group descriptions do not explain the exposure attribution or timing rules used for those counts.

These figures should be read as descriptive safety reporting for this trial, not as a complete estimate of safety. The record does not report event narratives, severity details beyond the serious-event classification, or a broader assessment of uncommon harms.

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

The primary result describes the difference in measured mouth dryness scores 15 minutes after dosing. The posted means were 4.51 cm for 3M spray and 4.6 cm for Biotene. The unadjusted recalculation gives a mean difference of 0.09 cm for Biotene relative to 3M, with a 95% confidence interval from -0.972 to 1.152. The sponsor-reported mixed-model estimate is -0.343, with a 95% confidence interval from -1.260 to 0.575. Both intervals include zero, and neither provides a narrow estimate of the difference.

These results do not establish that the products are identical. A result that is not clearly separated from zero can reflect a small difference, uncertainty around a difference, or both. The record does not report a threshold for a clinically important score difference, so it is not possible to determine which values in the intervals would be meaningful to participants. The sponsor labels its analysis non-inferiority, but the non-inferiority margin and its justification are not reported in the registry record. The label alone cannot demonstrate that a prespecified non-inferiority criterion was met.

The results also apply to the measured endpoint and timing, not necessarily to other dimensions of dry mouth or longer-term experience. The trial enrolled 40 participants and used a crossover design. Details of treatment periods, washout, missing observations, and the full sponsor model are not reported in the registry record, limiting independent assessment of the analysis.

Accordingly, the posted data support a cautious statistical description of the recorded scores and their uncertainty. They do not warrant medical advice or a claim that one treatment works or does not work. Broader conclusions would require context beyond the reported trial results, including the clinical importance of score differences and complete information about the analysis plan.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary question is framed as a paired comparison in a randomized crossover design. That structure can make within-participant differences informative, but it also means the analysis depends on features such as measurement period and treatment order. The registry identifies the design and the sponsor's mixed-model approach, yet does not provide enough model detail to reproduce or fully assess the sponsor's calculation. This illustrates why a label such as crossover or mixed models is not, by itself, a complete statistical methods description.

The primary estimate and its confidence interval also show why interpretation should not stop at a point estimate or p-value. The unadjusted recalculation is close to zero, but its interval spans values in both directions. The sponsor's reported interval likewise includes zero. The uncertainty is central to what can be said about the comparison; neither a nonsignificant p-value nor a non-inferiority label establishes equivalence.

The registry record further highlights the distinction between a trial's own planned sample size and retrospective planning illustrations based on an observed effect. The illustrations use explicit assumptions, but the original sample-size justification is not reported. The figures therefore cannot explain why the trial enrolled 40 participants or show whether its design was adequate for a specific target effect.

Finally, the number of posted outcomes makes multiplicity important. Without a reported strategy for interpreting many outcomes and time points, secondary findings deserve less weight than a prespecified primary result. Taken together, the case emphasizes careful attention to design, analysis alignment, interval precision, missing-data reporting, and the boundary between statistical evidence and clinical meaning.

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.

Important design and analysis details are not reported in the registry record. The crossover model is identified, but treatment durations, washout arrangements, randomization procedures, allocation concealment, and the participants or staff who were masked are not specified. The registry does not describe how the analysis handled period, sequence, or possible carryover effects. These details are relevant when interpreting within-participant comparisons.

The sponsor-reported mixed-model result is labeled non-inferiority, but the margin, rationale for that margin, and direction of the comparison are not reported. The model specification and p-value are also absent. This prevents an independent assessment of the non-inferiority analysis or direct reconciliation with the unadjusted summary-statistic recalculation. The primary endpoint is described as paired, but the correlation between each participant's measurements is not reported.

The primary population is described as intent to treat with Group Means Imputation, but the quantity and pattern of missing data, the imputation procedure, and sensitivity analyses are not reported. Multiplicity handling for the numerous outcome measures and time points is also not reported. A clinically important difference threshold for the visual analog score is absent, making it difficult to interpret the practical importance of estimates within the confidence intervals.

Safety reporting is descriptive and does not establish whether events were caused by either product. The record does not give event narratives or explain attribution in the crossover setting. The trial enrolled 40 participants, so the posted results provide limited information about uncommon events. These limitations concern what can be learned from the registry record; they do not establish that unreported procedures were not conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the Efficacy of 3M Dry Mouth Moisturizing Spray — NCT04186806.
• Registry record last updated 2024-10-02; status last verified 2024-09.
• Results first posted 2020-11-20.
• 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

NCT04186806 is a completed, randomized, single-masked crossover trial sponsored by Solventum US LLC. It enrolled 40 participants with xerostomia and compared 3M Dry Mouth Moisturizing Spray with Biotene Moisturizing Mouth Spray. The primary endpoint was a paired difference in mouth dryness visual analog scores 15 minutes after dosing.

The unadjusted recalculation estimates a mean difference of 0.09 cm for Biotene relative to 3M, with a 95% confidence interval from -0.972 to 1.152 and an unadjusted p-value of 0.868. The sponsor-reported mixed-model estimate was -0.343, with a 95% confidence interval from -1.260 to 0.575; its p-value is not reported. The record labels this analysis non-inferiority, but does not report the margin. Secondary results are unadjusted, and multiplicity, missing-data detail, and several design and model specifications are not reported in the registry record.