Experimental Pain Study to Assess Local Anesthetic Efficacy and Safety of CTY-5339 Anesthetic Spray in Normal Volunteers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Experimental Pain Study to Assess Local Anesthetic Efficacy and Safety of CTY-5339 Anesthetic Spray in Normal Volunteers (NCT02908620), a randomized phase 2 study. The primary outcome is Duration of Anesthesia as Measured by Pin Prick Test (PPT) for One Spray CTY-5339-A Compared to One Spray CTY-5339-CB.

2. Clinical Question

The study was designed to assess local anesthetic activity on cheek tissue in normal volunteers. Its stated purpose was to determine whether the combination of benzocaine and tetracaine had a longer duration of local anesthetic activity than benzocaine alone. This is a question about a measured response under an experimental pain-testing procedure, not a direct assessment of relief in people seeking treatment for a clinical condition.

The outcome was the duration of anesthesia recorded with a pin-prick test. The registry also lists heat-based quantitative sensory testing, onset measures, and responder percentages among secondary outcomes. Those measures address related but distinct features of the response: how long anesthesia was observed, how quickly it began, and whether a response was present at particular assessment times. The posted primary comparison is limited to one spray of each product, so it should not be treated as a result for every dose or regimen included in the study.

3. Trial Design

The registry describes a completed Phase 2, randomized, double-blind, partial cross-over, incomplete factorial study. The stated enrollment was 40, and the population was normal volunteers. The sponsor was Cetylite Industries. The study start date was 2016-12-07, and primary completion was 2017-04-02. The registry lists anesthesia as the condition.

The cross-over structure means that the listed treatment sequences involved testing a participant under more than one treatment condition, rather than assigning every participant to only one treatment for the whole study. The arm descriptions specify a 60 minute test session followed by a 4-14 day washout period before the next treatment session. The record describes sequences involving one spray of CTY-5339-A and one spray of CTY-5339-CB, as well as sequences comparing two sprays of CTY-5339-A with benzocaine plus vehicle control. This is consistent with the registry’s description of a partial cross-over and incomplete factorial design; it does not establish that every participant received every intervention.

Double masking and randomization are listed in the record. The precise randomization procedures, how treatment order was assigned, and how masking was maintained are not reported in the registry record. Likewise, the rationale for the partial cross-over or incomplete factorial structure is not reported in the registry record.

The primary outcome was measured in the modified intent-to-treat population defined in the registry. That definition required participants to have met inclusion and exclusion criteria before the blind was broken and either to have completed both 60 minute test sessions or to have returned to baseline values in all evaluation tests. The number of participants contributing to the primary outcome was 18 in each listed treatment group. The registry’s overall enrollment and the outcome-specific analysis populations describe different aspects of the trial and should not be conflated.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Modified Intent-to-Treat (mITT) population: all randomized subjects who, as documented prior to the breaking of the study blind: (1) met all the inclusion and exclusion criteria and; (2) either completed the two 60 minute test sessions or returned to baseline values in all evaluation tests.

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 Duration of Anesthesia as Measured by Pin Prick Test (PPT) for One Spray CTY-5339-A Compared to One Spray CTY-5339-CB, measured over Change in pain assessment from baseline (time of application) up to one hour post-application.

The primary endpoint was duration of anesthesia measured by the pin-prick test, in minutes, from application through one hour after application. It was intended to quantify how long a reduction in the pain response was observed after treatment. Participants were assessed at one-minute intervals during the first 5 minutes to capture onset. Starting at 5 minutes, assessments were scheduled at five-minute intervals through the one-hour time point.

The test used a 90-mm, 26-gauge pencil-point spinal needle. At screening, pin pricks were performed on each cheek and scored on a 0 to 10 Numerical Rating Scale, where 0 meant no pain and 10 meant severe pain. Eligibility required a minimum score of 3 on the last 2 pin pricks for each cheek, with one of those scores at least 4. This eligibility procedure helped establish that the experimental test could produce a measurable pain response before treatment assessment.

The registry states that participants with no indication of anesthesia by 10 minutes were considered treatment failures and had PPT discontinued. After onset, testing was also discontinued if anesthesia was no longer present at two consecutive evaluation time points from 10 minutes onward. These rules are relevant to interpretation because the recorded duration depended on the assessment schedule and the specified stopping criteria. The endpoint is therefore a protocol-defined measure of response during a controlled test, rather than a direct measure of everyday symptoms or a comprehensive measure of clinical benefit.

7. Results Posted in the Registry

• One Spray CTY-5339-CB: mean 16.40 versus 17.90 on control; difference -1.50 (95% CI -10.57 to 7.57), standardized effect d = -0.11; z-test p = 0.746.

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.

Duration of Anesthesia as Measured by Pin Prick Test (PPT) for Two Sprays CTY-5339-A Compared to One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P (Placebo)

• 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:
  • One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P: mean 13.50 versus 17.30 on control; difference -3.80 (95% CI -14.31 to 6.71), standardized effect d = -0.24; z-test p = 0.479.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P and the control. The interval gives the range of effects that remain compatible with the data.

Duration of Anesthesia as Measured by QST Heat for Two Sprays CTY-5339-A Compared to One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P (Placebo)

• 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:
  • One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P: mean 38.90 versus 46.80 on control; difference -7.90 (95% CI -19.72 to 3.92), standardized effect d = -0.42; z-test p = 0.190.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P and the control. The interval gives the range of effects that remain compatible with the data.

Duration of Anesthesia as Measured by PPT for One Spray CTY-5339-A Compared to Two Sprays CTY-5339-A

• 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:
  • Two Sprays CTY-5339-A: mean 17.30 versus 17.90 on control; difference -0.60 (95% CI -10.46 to 9.26), standardized effect d = -0.04; z-test p = 0.905.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Two Sprays CTY-5339-A and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover duration measured by pin-prick testing and heat-based quantitative sensory testing, comparisons involving two sprays of CTY-5339-A, and measures of onset and responder status. Across the duration comparisons with posted numerical results, the mean differences are not estimated precisely: the recalculated confidence intervals include zero, and the sponsor-reported ANOVA intervals also include zero where reported. The direction of the observed means is generally more favorable to CTY-5339-A regimens in comparisons with benzocaine plus vehicle, while the comparison between one and two sprays of CTY-5339-A is close and does not suggest a consistent gain from the additional spray in the observed PPT means.

This overall pattern is broadly compatible with the primary result in the limited sense that none of these comparisons provides a precise, statistically conclusive separation. Secondary findings do not independently overturn or confirm the primary comparison. They address different doses, tests, and outcome definitions, and the trial’s experimental setting remains the same.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for apparently notable results to arise by chance. Adjustment for multiplicity can control that concern, but whether any multiplicity procedure was prespecified or applied is not reported in the registry record. The record also does not report a hierarchy that would establish which secondary outcomes were confirmatory. Onset and responder outcomes are listed, but corresponding numerical estimates are not reported in the registry record. They cannot be inferred from the duration summaries, since response timing and duration are different features of the measured effect.

These secondary results are best treated as supportive descriptive context. A pattern across related measures can inform interpretation, but it is not equivalent to a prespecified combined test, and it does not provide the same evidential basis as a clearly specified primary analysis.

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

• Duration of Anesthesia as Measured by Pin Prick Test (PPT) for Two Sprays CTY-5339-A Compared to One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P (Placebo)
• Duration of Anesthesia as Measured by QST Heat for Two Sprays CTY-5339-A Compared to One Spray CTY-5339-CB in Combination With One Spray CTY-5339-P (Placebo)
• Duration of Anesthesia as Measured by PPT for One Spray CTY-5339-A Compared to Two Sprays CTY-5339-A
• Duration of Anesthesia as Measured by QST Heat for One Spray CTY-5339-A Compared to Two Sprays CTY-5339-A
• Onset of Anesthesia for PPT
• Onset of Anesthesia for QST Heat
• Percentage of Responders for PPT at Each Time Point
• Percentage of Responders for QST Heat at Each Time Point

9. Statistical Interpretation

10. Statistical Methods Explained

Continuous outcomes such as duration of anesthesia are commonly summarized by a mean and a standard deviation. The mean describes the group’s average observed duration, while the standard deviation describes how spread out individual observations were around that average. A standard deviation is not a confidence interval: it describes variation among observations, whereas a confidence interval describes uncertainty in an estimate such as a difference between group means.

What does the recalculated difference represent?

The simple recalculated contrast uses the posted group means and summarizes their difference without adjustment for other variables. For the primary comparison, its sign is defined as the mean for one spray of CTY-5339-CB minus the mean for one spray of CTY-5339-A. A negative value therefore indicates that the observed CTY-5339-CB mean was lower. The estimate is an unadjusted comparison of posted summary statistics; it is not the same as a participant-level analysis that models the cross-over structure, treatment sequence, period, or within-participant correlation.

That distinction matters in a cross-over study. Measurements from the same participant under different treatments are generally related, so an analysis that uses the paired structure may have different uncertainty from a calculation that treats the group summaries as independent. The registry reports an ANOVA analysis for the primary outcome, but the full model specification and the treatment of the cross-over structure are not reported in the registry record. Accordingly, the recalculation is useful as a transparent reading of the posted means and standard deviations, not as a replacement for the sponsor’s analysis.

How should the confidence interval be read?

A confidence interval gives a range of values compatible with the data and the analysis procedure at the stated confidence level. It communicates both the estimated direction and the precision of the estimate. If an interval includes zero for a difference, the data are compatible with no mean difference as well as with differences on either side of zero. An interval spanning zero is not proof that the treatments are identical; it indicates that the estimate does not pin down the direction with sufficient precision under that analysis.

The primary recalculated interval extends from -10.57 to 7.57 minutes. Its width reflects substantial uncertainty in the mean difference relative to the observed estimate. The interval does not tell the reader which value is most likely, and it does not establish whether every value in the range is clinically important. The registry does not report a threshold for a clinically important difference, so statistical compatibility cannot be translated into a judgment about clinical importance.

What does the p-value add?

A p-value describes how unusual the observed result, or a more extreme result, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it is not a measure of the size or practical importance of an effect. The recalculated primary p-value is 0.746, while the registry’s ANOVA analysis reports p = 0.322. These values arise from different analyses and should be read alongside their estimates and confidence intervals, not as standalone rankings of treatments.

Over-dispersion is a general statistical concern when variation in the data is greater than a model expects. If a method assumes less variability than is actually present, its standard errors can be too small and its intervals too narrow. The registry summarizes duration with standard deviations, but whether over-dispersion was assessed or how it was handled in the sponsor’s analysis is not reported in the registry record. For a continuous outcome, the practical issue is whether the assumed distribution and variance adequately represent the observed duration data. The posted aggregate summaries do not allow that question to be fully evaluated.

Why does the design affect the analysis?

Randomization helps prevent systematic differences in treatment assignment, while masking can reduce the influence of treatment knowledge on conduct and assessment. In a cross-over design, participants can serve as their own comparison, but the analysis may need to account for treatment order, period effects, and correlation between repeated measures. Washout periods are intended to separate treatment sessions; the record describes a 4-14 day washout. Whether carryover effects were assessed, and the statistical procedures used for that purpose, are not reported in the registry record.

The primary population definition also affects the interpretation. The registry’s modified intent-to-treat definition includes randomized subjects who met eligibility criteria before unblinding and either completed both test sessions or returned to baseline values in all evaluation tests. The record does not provide a detailed accounting of exclusions, missing measurements, or how each analysis handled incomplete data. Consequently, the estimand represented by the reported summaries cannot be fully reconstructed from the registry record alone.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the estimated difference. For the primary recalculation, the estimated mean difference is -1.5 minutes and the 95% confidence interval runs from -10.57 to 7.57 minutes. Because the interval includes zero, it is compatible with a lower mean for CTY-5339-CB, little or no difference, or a higher mean for CTY-5339-CB. The estimate is therefore not precise enough to settle the direction of the difference.

The interval’s width is important. It is broad relative to the point estimate and includes values that could represent meaningfully different durations in either direction. The registry record does not identify a clinical-importance threshold for this endpoint, so the interval cannot be divided into clinically meaningful and unimportant ranges using a registry-defined standard. Statistical uncertainty and clinical importance are related questions, but they are not interchangeable.

The sponsor’s reported primary interval, from -3.06 to 8.69, also includes zero. It is centered on the reported final-value estimate of 2.8 minutes and reflects a different analysis from the simple recalculation. Since the two estimates differ, the intervals should be understood as outputs from separate analytical approaches rather than combined or averaged. The record does not provide enough detail to reconcile them.

For the secondary comparisons, the recalculated intervals also span zero. This indicates that those summaries do not precisely establish the direction of the corresponding mean differences. A confidence interval is not a guarantee that the true effect lies within its limits; it is an inferential range generated under an analysis and its assumptions. In this study, the modest outcome-specific analysis groups and variability in duration contribute to uncertainty, but the registry record does not report a formal precision target or the original design assumptions.

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 illustration reports participants per arm for the continuous-outcome comparisons; it does not report total events. Read each row as a hypothetical planning scenario based on a stated fraction of the observed effect. The listed columns describe the participants per arm for 80% power and participants per arm for 90% power. In plain language, 80% power is the probability, under the planning assumptions and a specified true effect, that a study would meet its statistical significance criterion. The 90% column uses a higher target probability of detecting that effect.

The stated 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. The illustration is computed from the observed effect and is not the trial’s own original design justification; that justification is not reported in the registry record. These figures are not observed power.

Rows using a smaller fraction of the observed effect require more participants per arm in the planning illustration. This is a general feature of statistical planning: smaller differences are harder to distinguish from random variation, so a larger study is needed to attain the same target power, all else held constant. The same direction applies when comparing the 80% and 90% power targets: aiming for a greater probability of detecting the specified effect requires more participants per arm under the stated assumptions.

The values are illustrations, not a proposal for a new trial and not evidence that a particular effect is real. They inherit uncertainty from the observed effect estimate, which is imprecise in this study. For a cross-over design, the posted planning assumptions do not describe a paired or repeated-measures calculation; equal allocation between two arms and a normal approximation are stated, while design-specific planning details are not reported in the registry record. The curve should therefore be read as a visual counterpart to the same planning scenarios, not as an additional result from the trial.

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 = -1.500; pooled standard deviation σ = 13.883.
2. n = 2 × (1.96 + 0.842)² × 13.883² / -1.500² = 1,344.6, rounded up to 1,345 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 <- -1.5                      # observed difference in means
sigma <- 13.882542994711                     # 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(2908620)
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 = 1,345 (80% power), 1,801 (90% power)
 75% of observed effect: n per arm = 2,391 (80% power), 3,201 (90% power)
 50% of observed effect: n per arm = 5,379 (80% power), 7,201 (90% power)
power.t.test: 1345.6 
Simulated power at n = 1,345 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.

14. Analyses Reported by the Sponsor

The registry’s primary analysis is an ANOVA of mean difference in final values. It reports an estimate of 2.8 minutes, a 95% confidence interval from -3.06 to 8.69, and p = 0.322. The unadjusted recalculation from the posted group means and standard deviations instead estimates -1.5 minutes for CTY-5339-CB minus CTY-5339-A, with a 95% confidence interval from -10.57 to 7.57 and p = 0.746.

These estimates should be presented as separate analyses, not reconciled by changing the direction or choosing one result without explanation. The sponsor’s analysis may use participant-level data or model details not represented in the aggregate summaries, but the exact reason for the difference is not reported in the registry record. The record also does not describe the ANOVA model sufficiently to reproduce it from the posted summaries.

Both analyses have confidence intervals that include zero, so neither establishes a clear difference in the primary outcome. Their numerical estimates and precision differ, and the simple recalculation is explicitly an unadjusted summary-statistic calculation rather than a substitute for the sponsor’s model. The discrepancy flag is false, so there is no registry-identified discrepancy requiring one result to take precedence under the stated interpretation rules. The appropriate reading is to retain the sponsor’s reported result as the registry’s own analysis and use the recalculation only as a complementary, transparent check of the posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The trial includes a primary outcome and multiple secondary outcomes, with comparisons involving different formulations, spray amounts, and assessment methods. Testing several outcomes raises a multiplicity issue: even when no treatment difference exists, the chance of obtaining at least one apparently notable result can increase as more comparisons are examined. This general concern is especially relevant when secondary outcomes are interpreted after seeing their results.

The registry record does not report whether the study used a multiplicity adjustment, a hierarchical testing sequence, or another procedure to control the overall error rate across outcomes. It also does not report a prespecified hierarchy for the secondary outcomes. The p-values for the secondary analyses should therefore be read as unadjusted unless otherwise stated in the registry record. They are not equivalent to a single confirmatory test across all endpoints.

The primary outcome population is defined as a modified intent-to-treat population consisting of randomized subjects who met the inclusion and exclusion criteria before unblinding and either completed both 60 minute test sessions or returned to baseline values in all evaluation tests. That definition is informative, but the registry does not give a full participant flow for the primary analysis or explain all exclusions from the outcome-specific analysis groups.

Details of missing-data handling are not reported in the registry record. In particular, the record does not state how incomplete pin-prick assessments, treatment failures, discontinued testing, or missing measurements were represented in the primary analysis. It describes stopping rules for the PPT assessments, but does not provide enough information to determine their exact analytical consequences. The handling of missing data in the sponsor’s ANOVA is also not reported.

These omissions limit independent assessment of the analysis population, potential selection effects, and the robustness of the results to alternative assumptions about unobserved measurements. They do not establish that the analysis was inappropriate; they mean the registry record does not contain enough detail to evaluate those questions. A fuller protocol or statistical analysis plan would be needed to assess multiplicity control, missing-data strategy, and prespecification in greater depth.

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 lists serious adverse events for four treatment groups. The affected count is 0 in each listed group, and deaths are recorded as 0. The number at risk for serious adverse events is 20 in each group. The registry lists no serious adverse event terms.

For other adverse events, the record lists 0 affected in the CTY-5339-A one-spray group, 0 in the CTY-5339-A two-spray group, 1 in the CTY-5339-CB one-spray group, and 0 in the CTY-5339-CB plus placebo group. The number at risk for other adverse events is 20 in each group. The type or description of the other adverse event is not reported in the registry record.

These counts describe what was recorded for the listed groups; they should not be interpreted as proof that no unrecorded events occurred or as a guarantee about safety outside this study. The trial involved normal volunteers and the registry’s safety figures do not, by themselves, establish a safety profile for other populations, settings, or durations of exposure. The counts also do not answer the efficacy question.

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

The posted results describe a small experimental study of local anesthetic activity on cheek mucosal tissue in normal volunteers. The primary comparison asks whether one spray of CTY-5339-A and one spray of benzocaine alone differed in duration as measured by pin-prick testing. The observed group means are close relative to the uncertainty in their difference, and both the recalculated and sponsor-reported confidence intervals include zero.

This does not demonstrate that the treatments are identical. The intervals allow differences in either direction, and the registry does not report a threshold for deciding what magnitude would matter clinically. Nor do these results establish that one treatment is superior. The sponsor’s analysis reports an estimate in the opposite numerical direction from the simple recalculation, and the registry record does not explain the difference in analytical detail. Each result should be interpreted according to the analysis that generated it.

The study’s question and setting also define the limits of the conclusion. The endpoint is a protocol-defined measure of response to pin-prick testing, assessed repeatedly after application and subject to specified discontinuation rules. It is not a direct measure of pain relief in a patient population, and the study does not establish effects for other tissues, clinical situations, or treatment schedules.

The secondary outcomes extend the assessment to heat testing, other spray regimens, onset, and responder status. Their results are not a substitute for the primary endpoint, and multiplicity methods are not reported. Safety counts in the record show no serious adverse events or deaths in the listed groups, alongside one affected participant for other adverse events in one group. Those observations are limited to the study’s recorded exposure and participants.

In short, the registry reports estimates that remain uncertain about the direction and size of the primary difference. A lack of a statistically conclusive result is not proof of equivalence, and a numerical difference in observed means is not proof of a treatment effect.

18. Why This Trial Matters Statistically

This trial is statistically informative because its design combines repeated treatment sessions with a sensory outcome measured over time. Cross-over designs can make efficient use of within-participant comparisons, but that efficiency depends on accounting for correlation between repeated measurements and on handling period, sequence, and possible carryover effects appropriately. The registry identifies the design as partial cross-over and gives a washout period, while important details about the analysis of those design features are not reported.

The primary outcome also illustrates the difference between an observed group contrast and a precise estimate. The group means alone give a simple picture of the recorded durations; the confidence interval shows that the comparison remains uncertain. Reporting both the estimate and its uncertainty is more informative than relying on whether a p-value crosses a conventional threshold. The sponsor’s analysis and the simple recalculation further show why the analytical method and the direction used to define a difference matter.

The registry’s endpoint structure is another statistical issue. Duration, onset, heat response, and responder status capture related but nonidentical aspects of an experimental response. Testing many outcomes can complicate interpretation unless the analysis plan distinguishes confirmatory questions from exploratory ones. The record does not report a multiplicity strategy, so the secondary comparisons should not be treated as multiple independent confirmations.

Finally, the study separates experimental measurement from clinical interpretation. A controlled pain assessment can provide a reproducible way to examine response under specified conditions, but the meaning of that response depends on the population, protocol, and endpoint. The registry results are most useful when read with those boundaries in view, including the limited precision and the incomplete public detail on analysis and missing data.

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 outcome-specific analyses involve modest group sizes, and the duration measures show substantial variability relative to the estimated differences. This limits precision. The confidence intervals include zero and cover differences in either direction; the study therefore does not sharply locate the primary treatment contrast.

The cross-over design adds analytical considerations. The registry names a partial cross-over, incomplete factorial structure and describes a washout period, but it does not report enough detail to evaluate the handling of treatment sequence, period effects, within-participant correlation, or carryover. The sponsor reports an ANOVA, but the model specification is not reported in the registry record. The simple recalculation is based on group summaries and does not reproduce a participant-level cross-over analysis.

The primary analysis population is modified intent-to-treat rather than all randomized participants, using the registry’s stated eligibility and completion-or-return-to-baseline criteria. The registry record does not provide a full account of participant flow, reasons for missing observations, or the handling of incomplete assessments and treatment failures. This leaves uncertainty about how the analysis population and stopping rules affected the estimates.

Multiple secondary outcomes are listed, but multiplicity control and a testing hierarchy are not reported. Numerical results for onset and responder measures are not reported in the registry record. The available secondary results are therefore incomplete as a basis for assessing the full pattern of outcomes, and unadjusted comparisons should be treated cautiously.

Generalizability is also limited by the study population and setting: normal volunteers underwent a controlled cheek-tissue pain assessment. The registry record does not establish whether findings apply to patients or other clinical contexts. Finally, the primary endpoint is a protocol-defined sensory measure, and a threshold for clinical importance is not reported in the registry record. These limitations frame interpretation; they do not by themselves determine the direction of any treatment effect.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Experimental Pain Study to Assess Local Anesthetic Efficacy and Safety of CTY-5339 Anesthetic Spray in Normal Volunteers — NCT02908620.
• Registry record last updated 2019-07-02; status last verified 2019-06.
• Results first posted 2019-07-02.
• 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

NCT02908620 is a completed Phase 2 randomized, double-blind, partial cross-over study sponsored by Cetylite Industries. It enrolled normal volunteers and assessed local anesthetic activity after application to cheek mucosal tissue. The study began on 2016-12-07 and reached primary completion on 2017-04-02.

The primary outcome was duration of anesthesia measured by pin-prick testing through one hour after application. The posted mean was 17.9 minutes for one spray of CTY-5339-A and 16.4 minutes for one spray of CTY-5339-CB. The registry’s ANOVA reports a mean difference of 2.8 minutes, with a 95% confidence interval from -3.06 to 8.69 and p = 0.322. The simple unadjusted recalculation reports -1.5 minutes for CTY-5339-CB minus CTY-5339-A, with a 95% confidence interval from -10.57 to 7.57 and p = 0.746.

The intervals include zero, and the registry record does not report the detail needed to reconcile the different estimates. Secondary comparisons are also uncertain, and multiplicity and missing-data methods are not reported. No serious adverse events or deaths are listed in the safety record; one other adverse event is recorded in the CTY-5339-CB one-spray group.