Buffered Lidocaine in the Pediatric Dental Patient: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Buffered Lidocaine in the Pediatric Dental Patient (NCT04055116), a randomized phase 4 study. The primary outcome is Patient Reported Pain Perception.

2. Clinical Question

The trial also considers onset of soft-tissue anesthesia, a separate outcome relating to how soon anesthesia is observed after injection. This complements the pain question but measures a different aspect of the experience: reported pain is a subjective rating, whereas onset is recorded as elapsed time.

The central contrast is between two formulations administered to participants in a randomized sequence. The registry describes one occasion with one solution followed, after a minimum of one week, by the alternate solution. This crossover structure means that the comparison concerns both formulations within the trial’s sequence, rather than two independently assigned groups receiving only one formulation. The registry record does not report the age range, dental procedure details, or the precise circumstances under which pain and anesthesia were assessed. Those omissions limit how specifically the question can be generalized to particular pediatric patients or dental procedures.

3. Trial Design

The registry identifies NCT04055116, “Buffered Lidocaine in the Pediatric Dental Patient,” as a Phase 4 randomized, triple-masked crossover study sponsored by Geisinger Clinic. Its status is completed. The listed enrollment is 64. The recorded study start is 2019-11-11, and the primary completion date is 2021-12-17.

Participants were randomized to one of two treatment sequences: unbuffered lidocaine followed by buffered lidocaine, or buffered lidocaine followed by unbuffered lidocaine. The arm descriptions state that the alternate solution was administered after a minimum of one week. The record does not explain how the random sequence was generated, whether sequence allocation was balanced, or how the crossover period was accounted for in the statistical analysis.

The masking designation is triple, but the identities of the masked groups—such as participants, clinicians, or outcome assessors—are not reported in the registry record. Nor does the record describe whether masking was assessed or how it was maintained for the two formulations.

The primary outcome is patient-reported pain perception measured within 1 minute of anesthetic administration. The listed secondary outcome is onset of soft-tissue anesthesia, assessed from injection through 4 minutes post-injection at 15 second intervals. Posted outcome summaries report 55 observations for each formulation for both outcomes. In a crossover study, those condition-specific counts do not by themselves describe how many participants contributed complete paired observations or how missing observations were handled. That information is not reported in the registry record.

The registry does not report the original sample-size justification or the detailed analysis plan. The planning illustrations associated with the posted results are not a substitute for the trial’s original design assumptions.

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: Number of participants was high than the protocol enrollment number due to patients starting study but being removed by physician if patients could not follow study procedure.

First Intervention

Reasons for not completing this period:

Washout (14 Days)

Second Intervention (After 14 Days)

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 Patient Reported Pain Perception, measured over Within 1 minute of anesthetic administration.

The primary endpoint is patient-reported pain perception after administration of buffered or unbuffered lidocaine. It uses responses on the Wong-Baker FACES Pain Rating Scale, described in the registry as ranging from 0, “No Hurt,” to 10, “Hurts Worst.” Higher scores indicate greater reported pain, and the record says there are no sub-scores. The reported time frame is within 1 minute of anesthetic administration.

As a direct report of perceived pain, this outcome addresses the experience the trial aims to compare rather than relying only on an observer’s description. The registry summarizes the measure as a mean and standard deviation, treating the ratings as a continuous outcome for reporting and comparison. A mean gives the average score in each condition; the standard deviation describes how much individual ratings vary around that average.

Interpretation still depends on what the scale captures and when it is administered. A rating collected soon after injection reflects reported pain at that assessment point; it does not, by itself, measure later discomfort, satisfaction, or other aspects of dental care. The record does not report a threshold for a clinically important difference on this scale, so the statistical contrast cannot be translated into a stated threshold for meaningful change.

More generally, patient-reported outcomes are valuable when the target is a subjective experience, but they can be influenced by the assessment setting and how the question is presented. The registry does not provide further details about those procedures.

7. Results Posted in the Registry

• Buffered Lidocaine: mean 3.48 versus 3.52 on control; difference -0.04 (95% CI -1.24 to 1.16), standardized effect d = -0.01; z-test p = 0.948.

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.

Onset of Soft Tissue Anesthesia

• 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:
  • Buffered Lidocaine: mean 81.07 versus 102.21 on control; difference -21.14 (95% CI -63.15 to 20.87), standardized effect d = -0.19; z-test p = 0.324.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Buffered Lidocaine and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists onset of soft-tissue anesthesia as the secondary outcome. It addresses the timing of anesthesia after injection, whereas the primary outcome addresses children’s reported pain shortly after administration. These outcomes are related to the broader question of anesthetic administration but represent distinct concepts and should not be treated as interchangeable measures.

The posted secondary comparison is unadjusted, and the registry record lists no reported secondary analyses. Its result is therefore best read as exploratory context rather than as a separately confirmed finding. A secondary outcome can add useful information, but its evidential weight depends on whether it was prespecified, how it was analyzed, and how many outcomes or comparisons were considered. The record does not report the multiplicity strategy or a detailed analysis plan.

The secondary result does not replace or determine the interpretation of the primary pain endpoint. A difference in onset would not, by itself, establish a difference in pain, and the absence of a clear statistical signal for one outcome would not settle the other. Each outcome has its own measurement scale, source of variability, and timing.

In general, unadjusted secondary results carry less weight when multiple outcomes are examined because the chance of a nominally unusual result can increase across a set of tests. This is a general statistical consideration, not evidence that a particular adjustment was required or performed in this trial. The registry record does not report whether additional secondary outcomes were measured but not posted, nor does it give a multiplicity plan. As a result, the secondary endpoint can be considered alongside the primary result, but it should not be used as decisive confirmation of a treatment difference.

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

• Onset of Soft Tissue Anesthesia

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports continuous outcomes as means with standard deviations. A mean describes the average observed value, while a standard deviation describes dispersion among observations. These summaries are useful for comparing conditions, but they do not show the full shape of the outcome distribution, possible outliers, or the relationship between paired observations in a crossover trial.

What does a mean difference represent?

A mean difference expresses the average outcome in one condition relative to the other. For the primary outcome, the posted comparison is buffered lidocaine minus unbuffered lidocaine. On the scale used, a negative value indicates a lower mean pain rating for the buffered condition, while a positive value indicates a higher mean rating. The estimate is a sample-based contrast, not a claim that each participant experiences the same change.

For a crossover study, the analysis may use the fact that a participant receives both conditions. A paired analysis would take account of the within-participant relationship, which can affect the estimated uncertainty. The registry record does not report whether the comparison uses paired observations or how the treatment sequence and period are handled. Therefore, the posted contrast should not be assumed to represent a particular crossover model.

How should a confidence interval be read?

A confidence interval describes uncertainty around an estimated effect under the statistical method used. In general, an interval is compatible with a range of underlying effects, rather than identifying one exact value. Its width reflects the precision of the estimate: a wider interval leaves more uncertainty about the size and direction of the effect. A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it assign probabilities to individual values after the data have been observed.

For the primary comparison, the interval crosses zero. That means the posted interval is compatible with no average difference as well as with effects in either direction. The interval should be considered with the scale’s meaning and with any clinically important threshold. No such threshold is reported in the registry record.

What does the p-value add?

A p-value summarizes how unusual data at least as incompatible with a zero-difference model would be if that model and the analysis assumptions held. It is not the probability that the treatment formulations are the same, and it is not a measure of the size or importance of an effect. The registry lists an unadjusted p-value for the primary contrast. Because it is unadjusted, it does not account for testing multiple outcomes or comparisons.

Statistical significance is not the only consideration. An estimate can be small but imprecise, or large but uncertain. Interpretation should consider the estimate, interval, outcome scale, study design, and analysis assumptions together. A non-small p-value alone cannot establish that two formulations are equivalent.

Why can over-dispersion matter?

In general, over-dispersion means that observations vary more than a statistical model expects. When variability is not adequately represented, standard errors and confidence intervals may be too narrow, making uncertainty appear smaller than it is. The posted standard deviations show considerable spread in pain ratings, but the registry does not report a formal over-dispersion assessment or a model for the outcome distribution. The general concern is therefore relevant to evaluating assumptions, not evidence that a specific model failed.

For continuous outcomes, investigators may use methods that rely on assumptions about residual variation and distribution. In a crossover design, additional assumptions concern within-participant dependence and possible effects of treatment order or period. Those assumptions and checks are not reported in the registry record. The available summary statistics alone cannot verify them.

What do the sample-size illustrations mean?

The planning figures are illustrations based on fractions of the observed effect, not a reconstruction of the trial’s original sample-size calculation. Their stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row describes planning for a stated fraction of the observed effect. The columns describe participants per arm for 80% power and participants per arm for 90% power. For these outcomes, the figures are participants per arm, not total events.

Power is the probability, under a specified effect and model, of detecting that effect using the planned test at the chosen significance level. The 80% and 90% columns express different target probabilities for a future design under the stated assumptions. They are not properties observed after the trial, and they do not indicate the probability that the reported result is correct. The trial’s own sample-size assumptions and justification are not reported in the registry record.

All statistical explanations in this methods discussion are general unless they refer directly to the posted results or stated planning assumptions. The registry does not provide sufficient detail to determine the exact inferential model, missing-data procedure, or crossover-specific analysis used.

11. Confidence Intervals and Precision

The primary mean difference is -0.04, and its 95% confidence interval extends from -1.236 to 1.156. The interval crosses zero and covers effects favoring either condition in terms of average pain rating. Because higher scores indicate more pain, negative differences correspond to lower mean ratings with buffered lidocaine. The interval’s width means the point estimate alone should not be treated as a precise description of the underlying difference.

Precision concerns how narrowly the data locate an effect, not whether the effect is important. The interval does not identify a single exact effect, and the registry record does not supply a threshold for judging clinical importance on the Wong-Baker FACES scale. It is therefore not possible to use the interval to declare that all compatible effects are negligible or meaningful.

The primary standard deviations are 3.21 and 3.19, while the condition-specific summaries each report 55 observations. Those summaries do not indicate how strongly each participant’s two ratings were associated. That association could matter to the precision of a crossover comparison, but the registry does not report the paired-data analysis details.

The secondary outcome also has an interval that crosses zero, from -63.15 to 20.87 seconds for the posted mean difference. Its precision should be considered in light of the time measure’s variability and the analysis details, which are not reported. The displayed interval does not by itself establish that the formulations have the same onset time.

Confidence intervals provide more information about plausible effect sizes than a p-value alone, but they remain conditional on the analysis method and assumptions. For this trial, the absent crossover-model details and unreported clinical-importance thresholds limit how decisively the intervals can be interpreted.

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 figures are expressed as participants per arm for both 80% power and 90% power. They are not total event counts: the registry’s planning assumptions specify equal allocation between two arms, and these outcomes are continuous measures. For example, the row planning for 100% of the observed primary effect lists 100,467 participants per arm for 80% power and 134,497 participants per arm for 90% power.

These illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a different fraction of the observed effect as the effect to detect. The 80% column indicates the per-arm sample size associated with an 80% chance of detecting that specified effect under the assumptions; the 90% column gives the corresponding figure for a higher target chance. A higher target power generally calls for more participants under otherwise unchanged assumptions.

The rows also illustrate that smaller effects need more participants to detect. Planning for 75% or 50% of the observed effect therefore requires larger per-arm figures than planning for the full observed effect. This relationship is a general feature of study planning: a smaller signal is harder to distinguish from random variation.

These are planning illustrations based on the observed effect, not evidence about the probability that the completed trial detected an effect. They are not observed power. The original trial’s sample-size justification and design assumptions are not reported in the registry record, so the illustrations should not be read as the trial’s prespecified plan or as proof that its design was adequate for a particular target effect.

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 = -0.040; pooled standard deviation σ = 3.200.
2. n = 2 × (1.96 + 0.842)² × 3.200² / -0.040² = 100,466.6, rounded up to 100,467 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 <- -0.04                      # observed difference in means
sigma <- 3.20001562496185                     # 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(4055116)
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 = 100,467 (80% power), 134,497 (90% power)
 75% of observed effect: n per arm = 178,608 (80% power), 239,105 (90% power)
 50% of observed effect: n per arm = 401,867 (80% power), 537,986 (90% power)
power.t.test: 100467.6 
Simulated power at n = 100,467 per arm: 0.806 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when researchers test more than one outcome, time point, subgroup, or comparison. In general, conducting many tests without an adjustment or a prespecified hierarchy can increase the chance of at least one apparently notable result arising by chance. Whether and how to address that concern depends on the trial questions and analysis plan. The registry record does not report a multiplicity strategy, so the listed p-values should be understood as unadjusted rather than as part of a documented family-wise testing procedure.

The record identifies a primary outcome and one posted secondary outcome, but does not provide a complete statistical analysis plan. It does not report whether additional outcomes or time points were analyzed, whether outcomes were ranked in advance, or whether any adjustment was planned. The posted secondary comparison should consequently receive less confirmatory weight than a prespecified primary analysis.

Missing-data information is also limited. The posted outcome summaries report 55 observations for each formulation, while the listed enrollment is 64. The registry record does not explain the difference between those figures, say whether the same participants contributed observations in both conditions, or describe the reasons for unavailable observations. It does not report an imputation method, a missing-data sensitivity analysis, or whether the outcome summaries use an intention-to-treat, per-protocol, or other analysis population.

For crossover trials, the analysis population and completeness of paired measurements matter because each participant may contribute information under both conditions. The registry record does not report how incomplete pairs, sequence, period, or possible carryover were handled. These are not grounds to assume that the analysis was biased, but they leave important aspects of the analysis difficult to assess.

In general, a transparent account of outcome availability, analysis populations, and prespecified testing helps readers judge potential bias and the strength of inference. Those details are not reported in the registry record, so the posted summary estimates cannot answer every question about missingness or multiplicity.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports serious adverse events, other adverse events, and deaths by treatment sequence. For each sequence group, the posted figures show 55 participants at risk for the serious and other adverse-event categories, with 0 serious events, 0 other events, and 0 deaths recorded. The record lists no serious adverse-event terms.

These figures should be read as the events reported in the registry’s safety fields, not as proof that no unwanted effects occurred. The record does not describe how adverse events were defined, collected, monitored, or attributed to a formulation. It also does not explain whether the risk figures refer to a particular observation period or how crossover exposure was handled for safety reporting.

Zero recorded events in a category provides no estimate of the frequency or type of events that might occur outside the reported trial experience. Safety summaries are most informative when the event definitions, surveillance period, and completeness of reporting are clear; those details are not reported in the registry record. The event counts also do not establish a comparative safety difference between the formulations.

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

The posted primary result describes average pain ratings that are close between the two formulations, with an interval that includes possible effects in either direction. It does not establish that buffered and unbuffered lidocaine are equivalent, because equivalence requires a prespecified margin and an analysis designed to assess whether the full uncertainty interval falls within that margin. No equivalence margin is reported in the registry record.

Nor does the result establish that a clinically important difference exists. The point estimate is near zero, but the confidence interval includes a range of possible effects, and the record does not identify a threshold for a meaningful change on the pain scale. A non-significant unadjusted p-value is not evidence that the formulations produce exactly the same experience.

The findings are specific to the reported pediatric dental setting, formulations, measurement timing, and trial procedures. The registry record does not report an age range, detailed eligibility criteria, or procedure-specific information, so readers cannot determine how well the results apply to particular ages or dental situations. The crossover analysis details are also absent, limiting assessment of how the paired design was incorporated into the estimates.

The onset outcome concerns a separate aspect of anesthesia and should not be substituted for the primary pain measure. Likewise, safety counts with no recorded events in the listed categories do not establish the absence of all possible adverse effects. Taken together, the posted results offer a descriptive comparison with statistical uncertainty, rather than a definitive statement that one formulation is better, worse, or indistinguishable in every relevant respect.

In general, treatment conclusions require consideration of effect size, precision, measurement, design, and the relevance of the population. The registry results can inform that assessment, but unreported design and analysis details prevent a complete evaluation.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it uses a crossover design for a question about a subjective, short-term experience. A crossover can allow comparison of conditions within the same participant, which may be informative when participants differ in their general sensitivity or reporting style. That advantage depends on an analysis that appropriately reflects paired observations and considers sequence and period. The registry record does not report those analysis details, making the design’s statistical implications especially important.

The primary outcome also illustrates why effect estimates and uncertainty should be read together. The mean ratings are close, but the interval is broad enough to include differences in either direction. A point estimate alone can make a result appear more conclusive than the data warrant; a p-value alone can obscure the range of effects compatible with the estimate. The interval and the absence of a reported clinical-importance threshold both matter for interpretation.

The secondary onset measure highlights that trials can address multiple related but distinct questions. Pain perception and onset time are not interchangeable, and unadjusted secondary analyses should not be treated as independent confirmation of a primary finding. The registry record’s lack of a reported multiplicity plan makes that distinction relevant.

Finally, the planning illustrations show how strongly sample-size requirements can depend on the effect a future study aims to detect. Because smaller effects require more participants under the listed assumptions, planning figures based on an observed effect should not be mistaken for a record of the original design or a guarantee of evidential strength. The record does not report the original sample-size justification. Together, these features make transparent reporting of estimands, analysis populations, crossover methods, and uncertainty particularly important for this study.

18. Limitations

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

Several limitations specific to this trial follow from the registry information. First, although the design is identified as a randomized crossover, the record does not report the statistical method used to account for within-participant comparisons, treatment order, period, or possible carryover. The sequence descriptions include a minimum of one week between occasions, but the record does not explain whether that interval was chosen to address a particular carryover concern or how period effects were assessed.

Second, the record does not give the age range, eligibility criteria, dental procedure details, or further information about the participants. The trial is identified as involving pediatric dentistry, but the available description is not enough to assess how results might vary by age or procedure. The masking designation is triple, yet the roles of masked individuals and the success of masking are not described.

Third, the posted outcome summaries do not explain why the reported condition-specific observation counts differ from the listed enrollment, whether participants contributed complete paired data, or how missing outcomes were handled. The registry also does not report analysis populations, imputation, or sensitivity analyses. These omissions make it difficult to assess the influence of unavailable observations.

Finally, the record does not report a clinically important difference for the pain scale, the original sample-size calculation, a multiplicity plan, or a detailed statistical analysis plan. The posted estimates are therefore interpretable as summary contrasts, but the clinical importance and some assumptions underlying the inferential results remain uncertain.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Buffered Lidocaine in the Pediatric Dental Patient — NCT04055116.
• Registry record last updated 2023-04-07; status last verified 2023-03.
• Results first posted 2023-04-07.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04055116 is a completed Phase 4 randomized, triple-masked crossover study sponsored by Geisinger Clinic. It compares buffered and unbuffered lidocaine with epinephrine in pediatric dental patients. The listed enrollment is 64, and the recorded study dates are 2019-11-11 through primary completion on 2021-12-17.

The primary endpoint is patient-reported pain within 1 minute of anesthetic administration. The posted mean difference is -0.04, with a 95% confidence interval from -1.236 to 1.156 and an unadjusted p-value of 0.948. The registry also posts onset of soft-tissue anesthesia as a secondary outcome. The posted results should be interpreted with caution because crossover-analysis details, missing-data handling, the original sample-size rationale, and a multiplicity plan are not reported in the registry record.