A Study to Evaluate the Efficacy of a Stannous Fluoride Toothpaste With a Cetylpyridinium Chloride Mouthwash in Improving Gingival Health and Reducing Plaque Accumulation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy of a Stannous Fluoride Toothpaste With a Cetylpyridinium Chloride Mouthwash in Improving Gingival Health and Reducing Plaque Accumulation (NCT06660069), a randomized na study. The primary outcome is Overall Number of Bleeding Sites (NBS) at Week 12 (Toothpaste/Mouthwash Versus [vs.] Negative Control Toothpaste).

2. Clinical Question

3. Trial Design

This was a randomized, controlled, parallel-group, single-masked clinical study. The official title describes the study as examiner-blind and lasting 12 weeks. The registry lists enrollment of 199 participants, a completed status, and a phase entry of NA. The study started on 2024-11-18, with primary completion on 2025-03-11. HALEON is listed as the sponsor.

The primary efficacy comparison was between a regimen of stannous fluoride toothpaste followed by cetylpyridinium chloride mouthwash and negative-control sodium fluoride toothpaste. A reference toothpaste arm also used stannous fluoride toothpaste. The registry describes twice-daily brushing for 12 weeks in both toothpaste-only groups; for the combination group, the mouthwash followed each brushing. The primary result does not compare the combination regimen with the reference toothpaste arm.

The primary outcome was overall number of bleeding sites at Week 12. The registry reports least-squares means and standard errors for the two analyzed groups: 10.1 bleeding sites for the combination group and 24.1 for the negative-control group. The analyzed numbers were 63 and 59, respectively. These outcome-specific counts are not the same as the overall enrollment figure, and the registry specifies that only participants with data at the relevant timepoint were analyzed.

The registry does not report the randomization sequence method, allocation concealment procedure, or the identity of who was masked beyond the single-masking designation and examiner-blind description. The trial’s original sample-size assumptions, detailed protocol, and prespecified statistical analysis plan 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 199 participants were enrolled, 196 participants were randomized to treatment groups: 65 participants to the toothpaste/mouthwash group, 65 participants to the reference toothpaste group, and 66 participants to the negative control group. A total of 183 randomized participants subsequently completed the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The modified Intention-To-Treat (mITT) population comprised of all randomized participants who received at least one dose of investigational product and completed at least one-post Baseline efficacy assessment. Only those participants with data available at the specified timepoint were analyzed.

5. Baseline Characteristics

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

Population: Safety population- comprised all randomized participants who received at least one dose of investigational product.

6. Primary Endpoint

The registry lists the primary outcome as Overall Number of Bleeding Sites (NBS) at Week 12 (Toothpaste/Mouthwash Versus [vs.] Negative Control Toothpaste), measured over Week 12.

The primary endpoint was the overall number of bleeding sites at Week 12. A site counted toward the participant’s total when gingival bleeding was observed immediately after probing or within 30 seconds. The examination used an expanded bleeding index: a periodontal probe was placed in the gingival crevice and swept around each tooth, and six gingival areas around each tooth were assessed. A tooth site was considered evaluable when two-thirds of its natural surface was gradable.

This measure captures the presence of bleeding across assessed gingival sites and gives a count for each participant. Comparing group means summarizes the average burden of observed bleeding sites in each analyzed group; it does not describe every participant’s result or the distribution of individual responses. The registry reports least-squares means, which are model-based group estimates, together with standard errors. The comparison is expressed as an adjusted mean difference by the registry’s reported analysis.

Bleeding on probing is used in this trial as an efficacy measure for gingival health. The registry also lists plaque-related outcomes and other gingival measures as secondary outcomes. The endpoint definition establishes how the count was collected, but does not by itself establish how clinically important a particular difference is. A threshold for clinical importance is not reported in the registry record.

7. Results Posted in the Registry

• Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash): mean 10.10 versus 24.10 on control; difference -14.00 (95% CI -16.88 to -11.12), standardized effect d = -1.72; z-test p = <0.001.

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.

Interproximal NBS at Week 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)

• 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:
  • Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash): mean 4.50 versus 15.00 on control; difference -10.50 (95% CI -12.52 to -8.48), standardized effect d = -1.84; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall NBS at Week 6 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)

• 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:
  • Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash): mean 10.60 versus 25.00 on control; difference -14.40 (95% CI -17.42 to -11.38), standardized effect d = -1.67; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Interproximal NBS at Week 6 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)

• 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:
  • Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash): mean 5.10 versus 15.40 on control; difference -10.30 (95% CI -12.41 to -8.19), standardized effect d = -1.71; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Toothpaste/Mouthwash (SnF2 Toothpaste Followed by CPC Mouthwash) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results include Week 6 and Week 12 bleeding-site outcomes, with both overall and interproximal measures represented among the available results. For the secondary comparisons with negative-control toothpaste, the registry reports lower estimated bleeding-site counts in the combination group, with sponsor-reported adjusted differences in the negative direction. The pattern is consistent with the direction of the primary Week 12 overall result.

These outcomes provide related context, not independent confirmation of the primary finding. Overall and interproximal bleeding measures are linked aspects of gingival assessment, and assessments at different visits involve repeated measurement of related participants and outcomes. A consistent direction across related measures can help describe the broader pattern, but does not remove uncertainty about study conduct, measurement, missing data, or analysis assumptions.

The registry lists 18 outcome measures, 32 analyses, and 17 posted secondary outcomes. It does not report a multiplicity adjustment plan. When many outcomes or comparisons are examined, the chance of obtaining at least one apparently notable result by chance can increase. Unadjusted secondary p-values therefore generally carry less confirmatory weight than a prespecified primary analysis with an appropriate multiplicity strategy. The registry record does not establish which secondary analyses were prespecified or how the family of tests was handled.

The secondary results should be interpreted as supporting descriptive context around the primary comparison, rather than as a basis for making separate definitive claims for each endpoint. The primary result remains the clearest single inferential comparison in the record. Detailed clinical-importance thresholds for the secondary measures are not reported in the registry record.

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

• Interproximal NBS at Week 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Overall NBS at Week 6 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Interproximal NBS at Week 6 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Mean Overall Bleeding Index (Bl) at Weeks 6 and 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Mean Interproximal BI at Weeks 6 and 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Mean Overall Modified Gingival Index (MGI) at Weeks 6 and 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Mean Interproximal MGI at Weeks 6 and 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)
• Mean Overall Turesky Plaque Index (TPI) at Weeks 6 and 12 (Toothpaste/Mouthwash vs. Negative Control Toothpaste)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the reported mean difference represent?

A mean difference subtracts one group mean from the other according to the stated comparison direction. Here, the registry reports an adjusted mean difference of -14.0 bleeding sites for toothpaste followed by mouthwash versus negative-control toothpaste. A negative estimate indicates that the mean count was lower in the first named group. The group means are least-squares means, which are estimates from an analysis model rather than simply a statement about every participant’s individual count.

What does the Van Elteren Test contribute?

The sponsor’s reported analysis used a Van Elteren Test and described its estimate as an adjusted mean difference. The Van Elteren approach is a stratified rank-based comparison: it combines comparisons across strata while accounting for the stratification. In general, rank-based methods compare the ordering of observations rather than relying solely on the raw measurements’ distribution. The registry record does not report which stratification factors were used, how strata were formed, or the full model details. It is therefore not possible to reconstruct all features of the sponsor’s analysis from the posted results alone.

The registry labels the result as a superiority analysis. That designation describes the direction of the planned comparison type, not an independent measure of clinical importance. The estimate, interval, and p-value describe statistical evidence in the analyzed sample. Interpretation still depends on the study design, endpoint measurement, analysis population, missing observations, and assumptions.

How does the recalculation differ?

The recalculated comparison uses the posted group summaries to form a simple unadjusted mean difference and an approximate interval and p-value. For the primary comparison, it reports -14.0, an approximate 95% confidence interval from -16.88 to -11.12, and p <0.001. This is not a replacement for the sponsor’s analysis: it does not reproduce the stratified Van Elteren method or any adjustment not represented in the summaries. The pooled standard deviation used for the illustration is approximate because the group summaries provide standard errors rather than participant-level observations.

Standard errors describe the estimated sampling variability of group means. They are not the same as the spread of individual outcomes. The registry gives standard errors of 1.03 and 1.05 for the primary group means. Translating standard errors into a pooled outcome spread requires assumptions; consequently, the recalculated standardized effect and planning illustrations should be treated as approximations, not as outputs of the sponsor’s inferential procedure.

What does a confidence interval mean?

In general, a confidence interval is a range produced by a method that, under its assumptions and repeated use, would cover the underlying parameter at the stated rate. For this result, the sponsor’s reported 95% interval is -16.9 to -11.1 bleeding sites. It represents uncertainty about the estimated group contrast, not the range of individual participant outcomes and not a guarantee that the true effect lies in that particular interval.

An interval’s width conveys precision: narrower intervals indicate less uncertainty in the estimated contrast, while wider intervals indicate more. Precision depends on factors such as outcome variability, sample size, design, and analysis. The registry reports the interval and analyzed group sizes, but does not provide participant-level data or all model details needed to independently assess those factors in depth.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if a model assumes less variability than the data contain, which can in turn make confidence intervals too narrow and p-values too small. Count outcomes such as numbers of sites can have distributions that differ from simple model assumptions, depending on how counts vary across participants. The registry does not report a specific over-dispersion assessment for this endpoint, so no conclusion about whether it occurred can be drawn from the record.

What cannot be reconstructed?

The registry record does not report the trial’s original sample-size justification, its original power assumptions, interim analyses, missing-data strategy beyond the timepoint-specific analysis description, or a detailed multiplicity plan. It also does not report all protocol or model specifications. General statistical principles can explain why these details matter, but their use in this trial cannot be assumed. The post hoc planning illustrations based on the observed effect answer a different question from the original design calculation and should not be read as evidence about the study’s design or achieved power.

11. Confidence Intervals and Precision

The primary comparison’s reported 95% confidence interval extends from -16.9 to -11.1 bleeding sites around an adjusted mean difference of -14.0. The interval remains on the negative side of zero, so the reported analysis supports a lower estimated mean count in the combination group than in the negative-control group. The bounds also show that the estimate is not known with perfect precision: the interval includes a range of possible contrasts under the method’s assumptions.

The sponsor’s interval is rounded to one decimal place. The recalculated approximate interval is -16.88 to -11.12, based on the posted summaries and a simple unadjusted calculation. Its greater displayed precision does not mean it is more accurate; the calculation is approximate and does not reproduce the sponsor’s stratified analysis. The sponsor’s own analysis is the principal inferential result.

Confidence intervals concern uncertainty in a group-level estimate, not individual participant outcomes. They do not convey how much participant responses overlap, nor do they establish a clinical-importance threshold. The registry does not report such a threshold. Standard errors for the group means are 1.03 and 1.05, but these are measures of uncertainty in the means, not the variation among individual counts.

The recorded numbers analyzed at Week 12 were 63 and 59. Precision is influenced by sample size and outcome variability, among other design and analysis features. Participant-level outcome distributions, the full statistical model, and details of missing observations are not reported, limiting independent assessment of the interval’s sensitivity to those features.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size planning figures are participants per arm for this continuous outcome, not total events. They are planning illustrations derived from the observed comparison, rather than the original trial design calculation. The registry’s original sample-size assumptions and justification are not reported in the registry record.

The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. At 100% of the observed effect, the primary comparison illustration lists 6 participants per arm for 80% power and 8 participants per arm for 90% power. At 75% of the observed effect, it lists 10 and 13 participants per arm, respectively. At 50% of the observed effect, it lists 22 and 29 participants per arm.

In plain language, the 80% power column gives the planned number per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect is the true one. The 90% column describes the corresponding target at a higher probability of detection. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the assumed effect becomes smaller.

These values are not observed power. They are hypothetical planning calculations using the observed effect as an input, and the observed effect may not be the effect a future study would see. They do not establish that the trial was adequately powered under its original design.

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 = -14.000; pooled standard deviation σ = 8.122.
2. n = 2 × (1.96 + 0.842)² × 8.122² / -14.000² = 5.3, rounded up to 6 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 <- -14                      # observed difference in means
sigma <- 8.12231001624538                     # 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(6660069)
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 = 6 (80% power), 8 (90% power)
 75% of observed effect: n per arm = 10 (80% power), 13 (90% power)
 50% of observed effect: n per arm = 22 (80% power), 29 (90% power)
power.t.test: 6.4 
Simulated power at n = 6 per arm: 0.767 (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 sponsor’s reported primary analysis used a Van Elteren Test and gave an adjusted mean difference of -14.0 bleeding sites, with a 95% confidence interval from -16.9 to -11.1 and p < 0.001. The simple recalculation from the posted summary statistics gives a mean difference of -14.0, an approximate interval from -16.88 to -11.12, and p <0.001. Both estimates have the same direction and the same displayed point estimate, but the calculations are not identical procedures.

The recalculation is unadjusted and approximate. It uses group summary statistics and does not reproduce the sponsor’s stratified analysis. Its interval endpoints retain more decimal places than the reported sponsor interval, but that extra precision is only arithmetic display, not added certainty. The sponsor’s reported analysis is the appropriate primary result to interpret because it is the analysis posted for the trial.

The registry does not flag a discrepancy between the recalculation and the reported result. Differences in the interval formatting and in the reported p-value thresholds should not be treated as contradictory findings: one is a summary-statistic approximation and the other is the sponsor’s named analysis. The exact analysis plan and detailed model specifications are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 18 outcome measures, 32 analyses, and 17 posted secondary outcomes. With multiple outcomes, timepoints, and comparisons, multiplicity is a relevant statistical issue: examining many hypotheses can increase the chance that at least one result appears statistically notable even when there is no corresponding underlying difference. In general, a prespecified testing hierarchy or adjustment can help control that risk.

A multiplicity plan, including whether any adjustment was used for the secondary analyses, is not reported in the registry record. The reported secondary p-values should therefore be read cautiously and should not be treated as if they necessarily control the overall false-positive risk. The registry also does not report enough detail to determine which outcomes or analyses were prespecified in the protocol.

The primary population is described as modified intention-to-treat: randomized participants who received at least one dose and completed at least one post-baseline efficacy assessment. For the specified timepoint, only participants with available data were analyzed. The Week 12 primary outcome counts were 63 for the combination group and 59 for the negative-control group. The registry does not report why data were unavailable for other randomized participants, whether missingness differed by group, or whether sensitivity analyses were conducted.

In general, excluding participants without outcome data can affect estimates if missingness is related to outcomes or differs between groups. The record’s available-data approach does not by itself show that missingness biased the result, but the missing-data mechanism and any mitigation strategy cannot be assessed from the posted information. Interim analyses, the original analysis plan, and the trial’s sample-size justification are also 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 non-serious adverse event terms

The registry’s serious adverse event figures show 0 serious adverse events among 65 participants at risk in the toothpaste-and-mouthwash group, 0 among 65 in the reference toothpaste group, and 0 among 66 in the negative-control toothpaste group. It also reports 0 deaths in each group. No serious adverse event terms are listed.

These counts describe what was recorded in the registry for the groups and risk counts stated. Zero reported events does not establish that an event is impossible, nor does it alone establish equivalence in safety between groups. The trial’s group sizes and observation period constrain how much can be concluded about uncommon events. The registry does not give further detail about serious-event definitions, event ascertainment procedures, or a safety comparison analysis.

The record separately lists other adverse events affecting 19 participants in the combination group, 6 in the reference group, and 2 in the negative-control group. These are not serious adverse events and should not be conflated with the serious-event figures. The listed counts do not, by themselves, provide event type, severity, causality, or a formal between-group safety estimate.

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

The result means that, in the analyzed trial population, the sponsor estimated a lower average number of bleeding sites at Week 12 for participants assigned to stannous fluoride toothpaste followed by cetylpyridinium chloride mouthwash than for participants assigned to sodium fluoride toothpaste. The adjusted mean difference was -14.0 bleeding sites, with a 95% confidence interval from -16.9 to -11.1. This is a group-level comparison under the study’s design and analysis.

The result does not say that every participant in the combination group had fewer bleeding sites, or that each participant experienced the same change. Group means do not describe the full range of individual outcomes. The interval describes uncertainty in the estimated group contrast, not a prediction interval for an individual participant.

The comparison evaluates the combination regimen against sodium fluoride toothpaste. It cannot separate the contribution of the mouthwash from that of the stannous fluoride toothpaste, because those components were used together in the primary intervention group. Nor should the primary estimate be read as a comparison with the reference stannous fluoride toothpaste arm, which was not the primary control contrast.

The registry does not report a threshold for clinical importance, a complete account of missing data, or the detailed statistical plan. Statistical evidence and clinical importance are different questions: the reported interval and p-value describe the strength and precision of the estimated difference under the analysis, while the registry does not specify what size of difference would be meaningful to patients or clinicians.

The result applies to the studied participants, treatments, comparator, outcome definition, and Week 12 timeframe. It does not by itself establish what would occur under different regimens, in other populations, or over other periods. It is not medical advice and does not determine an appropriate individual treatment choice.

18. Why This Trial Matters Statistically

This trial offers a clear example of how a clinical comparison can be summarized through an endpoint definition, a group-level estimate, and an uncertainty interval. The primary outcome is a count of bleeding sites assessed using a specified probing procedure, and the reported mean difference gives the direction and magnitude of the estimated contrast in the units of that outcome. Keeping the unit visible helps prevent a statistical estimate from being mistaken for a general statement about health.

The record also illustrates why a sponsor-reported analysis and a summary-statistic recalculation need to be distinguished. Both give a point estimate of -14.0, but the sponsor’s Van Elteren analysis and the approximate unadjusted recalculation use different methods. The recalculation can be a useful cross-check, but it does not recreate the full analysis or supersede it.

The secondary outcomes add breadth to the reported assessment, while also raising the importance of multiplicity and prespecification. A consistent direction across related outcomes can inform interpretation, but multiple tests do not automatically provide independent confirmation. The absence of a reported multiplicity plan limits how strongly the secondary analyses can support confirmatory claims.

Finally, the registry’s description of the modified intention-to-treat population and timepoint-specific available data makes the analysis denominator important. Enrollment alone does not identify how many participants contributed to a particular endpoint. Reading the outcome counts alongside the population definition helps frame both the estimate and the remaining uncertainty.

19. Limitations

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

The registry record does not report the original sample-size justification or the assumptions used when the trial was designed. The planning illustrations based on the observed effect cannot fill that gap. Randomization details, allocation concealment, and the masking arrangements beyond the examiner-blind and single-masking descriptions are also not reported.

The primary outcome analysis includes participants with available data at the specified timepoint, within a modified intention-to-treat population. Reasons for missing outcomes, missingness patterns by group, and sensitivity analyses are not reported. As a result, the potential influence of unavailable observations cannot be assessed fully from the registry results.

The sponsor’s reported method is named as a Van Elteren Test, but the registry does not report its strata, full model specifications, or all analytic details. The independent recalculation is consequently approximate and unadjusted. It uses posted summaries rather than participant-level observations and should not be mistaken for a replication of the sponsor’s analysis.

The registry lists many outcomes and analyses but does not report a multiplicity strategy or establish which secondary analyses were prespecified. This limits the confirmatory interpretation of secondary results. A clinical-importance threshold for the primary or secondary endpoints is not reported either, so statistical evidence cannot be translated into a registry-defined judgment of practical importance.

The primary comparison concerns the combination regimen versus sodium fluoride toothpaste. It does not isolate the mouthwash effect, and the primary result is not a direct comparison against the reference stannous fluoride toothpaste arm. The record also does not report a detailed account of adherence or the complete mouthwash dosing description, limiting assessment of regimen implementation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy of a Stannous Fluoride Toothpaste With a Cetylpyridinium Chloride Mouthwash in Improving Gingival Health and Reducing Plaque Accumulation — NCT06660069.
• Registry record last updated 2026-03-18; status last verified 2026-02.
• Results first posted 2026-03-18.
• 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

NCT06660069 is a completed randomized, controlled, parallel-group study sponsored by HALEON, with an examiner-blind design and a 12-week treatment period. Enrollment was 199. The primary comparison was stannous fluoride toothpaste followed by cetylpyridinium chloride mouthwash versus sodium fluoride toothpaste in participants with clinically measurable plaque-induced gingivitis.

The primary endpoint was overall number of bleeding sites at Week 12. The sponsor reported an adjusted mean difference of -14.0 bleeding sites, with a 95% confidence interval from -16.9 to -11.1 and p < 0.001. The result describes the analyzed group comparison; interpretation is limited by unreported details on missing data, multiplicity, original sample-size planning, and the full statistical plan.