Clinical Trial Comparing Effectiveness of Buffered Versus Unbuffered Local Anesthetic in Children Ages 10-12 Years: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial Comparing Effectiveness of Buffered Versus Unbuffered Local Anesthetic in Children Ages 10-12 Years (NCT03562481), a randomized phase 4 study. The primary outcome is Mean Pain Scores Following Injection.

2. Clinical Question

This is a comparison of two formulations and concentrations as used in the trial; it does not isolate buffering from concentration. The registry’s stated null hypothesis for pulpal anesthesia concerns no difference between the conditions, while the posted primary outcome is injection pain. Those are related study questions, but they are distinct outcomes. The page therefore focuses on the pain scores and does not treat them as a direct measure of every aspect of anesthetic performance.

3. Trial Design

The registry describes a randomized, triple-masked, crossover study sponsored by the University of North Carolina, Chapel Hill. It is listed as phase 4 and completed. The study title identifies children ages 10-12, and enrollment is listed as 26. The registry gives a start date of 2018-07-24 and a primary completion date of 2019-06-30.

In a crossover design, participants receive more than one study condition, so comparisons can involve observations from the same people under different conditions. Here, the registry describes two treatment sequences: buffered anesthetic followed by unbuffered anesthetic, or unbuffered anesthetic followed by buffered anesthetic. A minimum one-week washout period was specified between injections. Randomization was used to assign the sequence, and masking is listed as triple. The record does not explain which roles were masked.

The primary outcome summaries show 25 participants in each anesthetic condition. The primary outcome description notes that one participant did not complete the second intervention and was excluded from the analysis. The registry does not provide further detail about the participant’s first-period data or how the crossover observations were handled in the primary analysis.

The study description identifies a wider set of aims: pain on injection, time to onset, time to recovery, blood lidocaine levels 15 minutes after administration, and duration of pulpal anesthesia. The registry lists nine outcome measures and nine analyses, but no secondary outcomes are posted in the information used for this page. The original protocol’s sample-size rationale, the details of the masking procedures, and the planned statistical analysis are not reported in the registry record. The stated washout interval and design label describe the study structure; by themselves, they do not establish how possible period or carryover effects were evaluated.

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.

First Intervention

Reasons for not completing this period:

Washout

Second Intervention

Analysis population for the primary outcome, as defined in the registry: One participant did not complete the second intervention and was excluded from the data analysis.

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 Mean Pain Scores Following Injection, measured over Within 10 minutes of injection.

The primary endpoint is mean pain score following injection, measured within 10 minutes of injection. Participants reported perceived pain verbally using a Likert scale from 1-10, with 1 defined as no pain and 10 as the worst pain imaginable. Lower scores indicate less reported pain. The registry specifies the mean as the summary measure and standard deviation as the measure of spread.

Pain on injection is used as a patient-reported measure of immediate experience. It addresses one of the study’s stated domains and gives a direct account of how participants rated the injection, rather than a clinician’s rating or a laboratory measure. Because the outcome is a score on a bounded scale, the mean summarizes the group’s average response, while the standard deviation describes how dispersed the scores were around that average. Neither statistic shows every individual response, and the mean alone does not describe the shape of the score distribution.

The posted mean was 3.0 for the buffered condition and 3.3 for the unbuffered condition. The registry’s description of the endpoint says lower scores correspond to less pain; these values should therefore be read as group summaries of reported pain, not as measurements of anesthetic onset, duration, blood concentration, or pulpal anesthesia. Those other domains are separate study questions. Their results are not reported in the registry record.

The endpoint is useful for comparing the observed pain ratings under the two conditions, but interpretation also depends on the design and analysis. Since this was a crossover trial, the order of conditions and the within-participant nature of the design matter to statistical inference. The posted summaries do not show the paired participant-level differences, so they cannot on their own convey how each participant’s scores changed between conditions.

7. Results Posted in the Registry

• Unbuffered Anesthetic: mean 3.30 versus 3.00 on control; difference 0.30 (95% CI -0.65 to 1.25), standardized effect d = 0.18; z-test p = 0.535.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry presents two kinds of results that should be kept distinct: the sponsor’s reported analysis and a simple unadjusted recalculation based on posted summary statistics. The recalculation helps readers see the estimated difference and its uncertainty using the displayed group means and standard deviations. It does not reproduce every feature of the original trial analysis, and the registry’s crossover design makes that distinction important.

What does the mean difference represent?

The mean difference is the difference between the posted average pain scores, expressed in the order unbuffered minus buffered. The posted means are 3.3 and 3.0, respectively, and the recalculated mean difference is 0.3. A positive value in this direction indicates that the unbuffered group summary is higher. Since lower scores represent less reported pain, the direction of the estimate is descriptive; it does not establish a treatment effect or show that the difference matters to participants.

A mean is a summary of the observations, not a description of every score. The standard deviations are 1.5 for unbuffered anesthetic and 1.9 for buffered anesthetic. Standard deviation describes the spread of participant scores around the mean. A difference between means needs to be interpreted alongside that variability and the amount of information available. The displayed summaries do not provide the individual scores or the paired differences for participants who received both conditions.

What does the confidence interval add?

A confidence interval gives a range of values that are compatible with the data and the statistical procedure used, under its assumptions. It is not a range that contains a fixed percentage of individual participants’ pain scores, and it does not assign a probability to a particular treatment effect after the data have been observed. The recalculated interval for the mean difference crosses zero. That means the interval includes no difference, while also allowing differences on either side. Its breadth indicates that the estimate is not highly precise.

The p-value of 0.535 belongs to the simple unadjusted recalculation. In general, a p-value describes how unusual data at least as discordant with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it is not a measure of the size or importance of a difference. Here, the p-value does not provide strong evidence against a no-difference null in that calculation. It cannot establish that the conditions are equivalent.

Why does the crossover design matter?

In general, a crossover design allows each participant to receive both conditions, so a treatment comparison can use within-participant information. That pairing can be informative because each participant can serve as their own comparison. It also means that analyses may need to account for the order in which conditions were received and the period in which each outcome was measured. A washout period is intended to separate treatment periods, but the existence of a washout does not itself establish that carryover was absent or that period effects were addressed.

The registry describes random assignment to treatment sequence and a minimum one-week washout. It does not report the statistical model used for the sponsor’s analysis, how paired observations were treated, whether sequence or period was included, or whether carryover was assessed. The simple recalculation uses posted summary statistics rather than participant-level crossover data. It should therefore be considered an unadjusted summary-based comparison, not a full reconstruction of the crossover analysis.

How should the sponsor analysis be read?

The sponsor reports an ANOVA with F statistic 0.80 and p-value 0.38, and classifies the analysis as equivalence. ANOVA is a general method for comparing means across groups or conditions, with its exact interpretation depending on the model and design. For a crossover trial, the model specification is important because observations from the same person are related. The registry does not give the model terms, degrees of freedom, confidence interval, or equivalence margin. Those omissions limit independent assessment of the reported equivalence analysis.

Equivalence testing asks whether the treatment difference is sufficiently close to zero according to a prespecified acceptable range. In general, that range must be defined before examining results, and the uncertainty around the estimated difference must be evaluated relative to it. Without the margin and the relevant interval, the registry’s equivalence label cannot be fully evaluated. It should not be interpreted as proof that the two conditions produce the same outcome.

What is over-dispersion, and is it?

In general, over-dispersion means that observed variability is greater than a statistical model expects. When a model assumes less variability than the data contain, its uncertainty estimates can be too small, making results appear more precise than they are. The posted primary outcome is a continuous score summarized by means and standard deviations, and the registry does not report an over-dispersion assessment. This concept is a general consideration, not a reported finding from this trial.

More broadly, the registry record does not report the original sample-size justification, full statistical plan, missing-data procedure, or detailed analysis population definition. The study lists nine analyses and nine outcome measures, but the other outcome results are not posted. Those absences mean readers should avoid assuming that the simple recalculation captures all planned analyses or that the available results answer the full set of study aims.

10. Confidence Intervals and Precision

The recalculated mean difference is 0.3, with a 95% confidence interval that extends from a value below zero to a value above zero. The interval therefore includes no difference between the conditions. It also permits a range of differences in either direction, so the point estimate alone gives an incomplete picture. The recalculation’s p-value is 0.535; this does not provide strong evidence against a no-difference null under that unadjusted calculation.

Precision concerns how narrowly the data estimate a quantity. A narrow interval would indicate a more precise estimate, while a wide interval would leave greater uncertainty about the size and direction of the difference. Here, the interval does not support a precise estimate of the treatment contrast. Its crossing of zero is not proof that the true difference is zero; nor does it demonstrate equivalence. Equivalence requires a defined margin and a suitable analysis, and the registry does not report the margin.

The standard deviations of the posted scores are 1.9 for buffered anesthetic and 1.5 for unbuffered anesthetic. These describe the spread of observed scores within each condition, while the confidence interval describes uncertainty about the estimated mean difference. They answer different questions. The posted group summaries cannot show the distribution of individual paired differences or how much within-person correlation contributed to the crossover comparison.

The sponsor’s reported ANOVA result gives an F statistic of 0.80 and p-value of 0.38, but no confidence interval is posted for that result. Because the registry does not report the sponsor’s model details or equivalence margin, the precision and interpretation of that analysis cannot be fully assessed from the record. In general, the confidence interval is more informative than a p-value alone about the range of effect sizes compatible with the data, but that interval must correspond to an appropriate analysis of the design.

11. Planning a Similar Trial: Sample Size

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

The sample-size table is a planning illustration derived from the observed mean difference, not a report of the trial’s original sample-size calculation. The figures are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For the rows based on a fraction of the observed effect, the effect to detect is the stated fraction of that observed effect.

The table gives planning results for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For 100% of the observed effect, it lists 512 participants per arm for 80% power and 685 participants per arm for 90% power. For 75% of the observed effect, it lists 909 participants per arm for 80% power and 1,217 participants per arm for 90% power. For 50% of the observed effect, it lists 2,045 participants per arm for 80% power and 2,737 participants per arm for 90% power.

In plain language, the 80% power column gives the planned number per arm for a study with an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real. The 90% power column uses a higher chance of detection and consequently gives larger planning numbers. Smaller effects need more participants to distinguish them from random variation with the same planned power. The table is not observed power and does not describe what the completed trial achieved. The trial’s own original sample-size assumptions are not reported in the registry record. The curve on the page visualizes this planning relationship; it does not add observed trial participants or alter the posted results.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.300; pooled standard deviation σ = 1.712.
2. n = 2 × (1.96 + 0.842)² × 1.712² / 0.300² = 511.0, rounded up to 512 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 <- 0.3                      # observed difference in means
sigma <- 1.71172427686237                     # 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(3562481)
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 = 512 (80% power), 685 (90% power)
 75% of observed effect: n per arm = 909 (80% power), 1,217 (90% power)
 50% of observed effect: n per arm = 2,045 (80% power), 2,737 (90% power)
power.t.test: 512 
Simulated power at n = 512 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Analyses Reported by the Sponsor

The sponsor’s posted analysis is an ANOVA with F statistic 0.80 and p-value 0.38. The registry classifies it as an equivalence analysis. The simple recalculation from the posted group summaries gives a mean difference of 0.3 and p-value of 0.535, with a confidence interval that crosses zero. These results come from different approaches and should not be treated as interchangeable.

The recalculation is an unadjusted comparison based on the posted means and standard deviations. It does not use participant-level paired differences or reconstruct the full crossover model. The sponsor’s analysis may have used design features not visible in the registry entry, but the model details are not reported in the registry record. The record’s discrepancy indicator is false, so there is no flagged disagreement between the posted sponsor result and the recalculation that would require a discrepancy warning.

The equivalence label needs particular care. To evaluate equivalence, readers need the prespecified margin and an uncertainty estimate assessed against that margin. Neither is reported for the sponsor’s result. The reported p-value by itself cannot establish equivalence, and the recalculated non-significant result cannot do so either. The sponsor analysis remains the reported trial analysis; the recalculation is a transparent supplementary summary-based estimate, not a replacement for it.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists nine outcome measures and nine analyses, but the results give detail for the primary outcome of mean pain scores following injection. No secondary outcome results are posted in the registry record. The study description mentions several other domains, including onset, recovery, blood lidocaine levels, and duration of pulpal anesthesia, but their observed results and analyses are not available.

When a study evaluates multiple outcomes or makes multiple statistical comparisons, the chance of at least one apparently unusual result can increase. Statistical procedures for multiplicity can account for that issue, but the appropriate approach depends on which outcomes were primary, which were secondary, and how the hypotheses were planned. The registry does not report whether multiplicity adjustment was planned or applied. It is therefore not possible to assess how the nine listed analyses relate to one another or whether the reported p-values were adjusted.

The primary outcome description says that one participant did not complete the second intervention and was excluded from the data analysis. The posted summaries show 25 participants for each anesthetic condition, while enrollment is listed as 26. The registry does not report whether the participant’s first-period observation was retained elsewhere, how incomplete crossover data were handled, or whether any imputation or sensitivity analysis was performed. Further details about other missing measurements are not reported in the registry record.

The analysis population is also not fully described. The record does not state whether the sponsor used an intention-to-treat, per-protocol, or other defined population for the equivalence analysis. Nor does it report the handling of protocol deviations or analysis exclusions beyond the note about the participant who did not complete the second intervention. These details matter because analysis choices can affect both the estimate and its uncertainty, particularly in a crossover study where incomplete participation may leave a participant without a complete pair of observations.

Finally, the registry does not provide the original statistical plan or sample-size justification. Without those materials, readers cannot determine which analyses were prespecified, how missing data and multiplicity were intended to be addressed, or whether the posted results represent all planned analyses. These are reporting limitations, not evidence that any particular procedure was or was not used.

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 adverse-event figures list zero serious adverse events in the buffered group, with 25 at risk, and zero in the unbuffered group, with 26 at risk. The registry also lists zero other adverse events in both groups, with 25 at risk for buffered anesthetic and 26 at risk for unbuffered anesthetic. Deaths are listed as zero for both conditions. No serious adverse-event terms are listed.

These are counts in the registry record, not evidence that the risk of an event is zero. The numbers describe what was recorded among the listed at-risk participants during the study as reported. The record does not provide additional detail about how adverse events were defined, collected, monitored, or attributed to a condition. It also does not explain why the at-risk counts differ between conditions in this crossover study.

Zero recorded events in a study of this size should be interpreted with appropriate caution: uncommon events may not occur in a limited study, and the absence of a recorded event does not establish the absence of risk. These figures are a description of the posted safety data, not a basis for medical advice or a broad comparison of safety between formulations.

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

The posted primary results show mean pain scores of 3.0 for buffered anesthetic and 3.3 for unbuffered anesthetic, on a scale where lower values represent less reported pain. The simple unadjusted recalculation estimates a mean difference of 0.3 for unbuffered compared with buffered anesthetic. Its confidence interval crosses zero, and its p-value is 0.535. These data describe the observed summaries and the uncertainty around that recalculated comparison.

The result does not establish that the formulations are the same, nor does it demonstrate equivalence. A failure to find strong evidence against a no-difference hypothesis is not proof of no difference. An equivalence conclusion needs a prespecified margin and an analysis showing that the uncertainty lies within that margin; the registry does not report the margin for the sponsor’s analysis. The sponsor’s ANOVA is classified as equivalence, but the model details and supporting interval are not reported in the registry record.

The result also does not answer every question in the study description. Injection pain is a subjective endpoint recorded within 10 minutes. It is not a substitute for measurements of onset, recovery, blood lidocaine concentration, or pulpal anesthesia duration. Secondary results for those domains are not reported. The record therefore does not support conclusions about those outcomes from the pain scores.

Because the design was a crossover, interpreting the comparison ideally requires information about paired responses and treatment sequence. The registry describes randomized order and a minimum one-week washout, but does not report the sponsor’s model or how period and carryover considerations were handled. The summary-based recalculation cannot show the within-participant pattern.

In statistical terms, the posted pain data are consistent with a range of possible differences and are not highly precise. They should be read as a limited estimate from the analyzed observations, rather than a definitive statement about clinical importance or treatment choice. Nothing in this statistical interpretation is medical advice.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates how design, outcome measurement, and reporting all shape interpretation. A crossover design can compare conditions within the same participant, which can be valuable when outcomes vary considerably between people. At the same time, a crossover analysis needs to address the ordering of conditions and the fact that measurements from one participant are related. The registry describes random sequence assignment and a minimum one-week washout, but does not provide enough analysis detail to assess how those features entered the sponsor’s model.

The primary outcome is participant-reported pain on a Likert scale, and the registry provides group means, standard deviations, and sample sizes. That makes a basic summary-based comparison possible. The mean difference and confidence interval are more informative together than a p-value alone: the point estimate describes the observed direction and size, while the interval shows that the estimate remains uncertain. The interval crossing zero should not be converted into a claim of equality.

The sponsor’s analysis is labeled as equivalence, which highlights a separate statistical question from conventional testing for any difference. Equivalence requires a clinically justified margin and uncertainty assessed against that margin. Since the margin and model details are not reported in the registry record, the label cannot be independently evaluated. This is a useful reminder that a statistical label does not replace the information needed to judge the analysis.

Finally, the record distinguishes a primary result from a broader set of study aims. Nine outcomes and nine analyses are listed, but secondary results are not posted. The missing analysis and outcome details limit what readers can infer about the full study. Careful interpretation means keeping the result tied to the specific endpoint and analysis available, and recognizing where the registry record does not show enough to answer a wider question.

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 are specific to interpreting this registry entry. First, the trial is a crossover study, but the posted group summaries do not include participant-level paired differences. The registry describes randomization to order and a minimum one-week washout, yet it does not report how the sponsor’s analysis handled the within-participant structure, treatment period, sequence, or potential carryover. The summary-based recalculation should not be mistaken for a full crossover analysis.

Second, one participant did not complete the second intervention and was excluded from the primary pain analysis. The record does not say whether that participant contributed data from the first condition, why the second intervention was not completed, or how incomplete data were handled in the sponsor’s analysis. It gives no imputation or sensitivity-analysis details. This limits assessment of how the missing second-period information may affect the result.

Third, the sponsor’s analysis is classified as equivalence, but the registry does not report the equivalence margin, confidence interval, or full model specification. The result therefore cannot be independently assessed as an equivalence test. The simple recalculation offers a separate unadjusted estimate, but it does not resolve this gap.

Fourth, the primary endpoint is self-reported pain on a 1-10 Likert scale. The posted mean and standard deviation summarize the outcome but do not show the full score distribution or individual responses. The registry does not report secondary results for the other study domains, despite listing nine outcome measures and nine analyses. Multiplicity handling, the original sample-size justification, and the prespecified analysis plan are also not reported in the registry record.

These are limits on what can be concluded from the record, not evidence that unreported methods were absent. They mean that interpretation should remain focused on the posted pain summaries and the analyses whose details are available.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Clinical Trial Comparing Effectiveness of Buffered Versus Unbuffered Local Anesthetic in Children Ages 10-12 Years — NCT03562481.
• Registry record last updated 2020-06-25; status last verified 2020-02.
• Results first posted 2020-06-25.
• 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

This completed phase 4 study was a randomized, triple-masked crossover comparison of buffered 1% and unbuffered 2% lidocaine, both with 1:100,000 epinephrine, in children ages 10-12. Enrollment was 26. The registry describes two treatment sequences with a minimum one-week washout between injections.

The primary outcome was verbally reported pain within 10 minutes of injection, scored from 1-10. Posted mean scores were 3.0 for buffered anesthetic and 3.3 for unbuffered anesthetic, with 25 observations in each condition. One participant did not complete the second intervention and was excluded from the primary analysis.

The sponsor reports an ANOVA with F statistic 0.80 and p-value 0.38, classified as an equivalence analysis. A simple unadjusted recalculation gives a mean difference of 0.3 and p-value of 0.535, with an interval that crosses zero. The equivalence margin, full analysis model, secondary results, and original sample-size justification are not reported in the registry record.