The Anesthetic Efficacy of 3% Mepivacaine Plus 2% Lidocaine With 1:100,000 Epinephrine for Lower Jaw Dental Injections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Anesthetic Efficacy of 3% Mepivacaine Plus 2% Lidocaine With 1:100,000 Epinephrine for Lower Jaw Dental Injections (NCT01574807), a randomized phase 4 study. The primary outcome is Number of Participants Achieving Pulpal Anesthesia Success..

2. Clinical Question

The trial addresses whether the number of participants reaching and maintaining the specified maximal response differs between the two sequences. The primary outcome is a participant count, not a continuous measure of numbness or a measure of pain intensity. The registry’s summary frames the comparison as testing whether the mepivacaine-then-lidocaine sequence differs in effectiveness from the lidocaine-then-lidocaine sequence.

The endpoint definition is tied to an electric pulp tester assessment of lower-jaw teeth. Success required reaching the maximum device level by the fifth testing period, identified in the record as 17 minutes after injection, and maintaining that response for the rest of the testing period. The stated observation timeframe is 60 minutes per injection sequence.

The comparison is within participants: the registry describes a repeated-measures design in which each participant received both interventions. That feature matters statistically because observations from the two sequences in the same person are paired rather than independent. The registry record does not report further details about how the order was assigned or managed beyond identifying the study as randomized and crossover.

3. Trial Design

The registry identifies this as a Phase 4, randomized, double-blind crossover study sponsored by Ohio State University. It is marked completed and records enrollment of 100 participants. The recorded start is 2012-05, and primary completion is 2013-05.

The two interventions are sequences of injections. One sequence begins with mepivacaine plus lidocaine and then uses lidocaine plus lidocaine; the other begins with lidocaine plus lidocaine and then uses mepivacaine plus lidocaine. The registry describes a single group of participants, with each participant receiving both interventions and serving as their own control. This is the defining comparison structure: results from the two sequences are related because they come from the same participants.

The study is marked double-blind, but the registry record does not report who was masked or how masking was maintained. The record does not report the crossover sequence allocation details, a washout period, or other period-management procedures. Those omissions prevent a fuller assessment of possible order or carryover effects from the registry information alone.

Enrollment and the posted outcome counts are both 100 for each intervention. In a crossover study, these figures should not be read as evidence of separate groups of 100 participants. The arm descriptions state that a single group received both interventions, and the posted group counts are consistent with evaluating both sequences in the same participant set.

The registry lists one primary outcome measure and one reported analysis. No secondary outcomes are posted in the record. The trial’s own sample-size justification and original design assumptions are not reported in the registry record. Consequently, the enrollment figure can be described, but the registry does not establish why that target was chosen or what precision or power was anticipated when the trial was planned.

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: No subjects were excluded from the study.

First Appointment

Wash Out Period 2 Weeks

Second Appointment

Analysis population for the primary outcome, as defined in the registry: Success of anesthesia was determined by subject achieving maximal level (80) with testing device by 5th testing time period (17 min.) following injection and maintaining that maximal response for the remainder of the testing time.

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 Number of Participants Achieving Pulpal Anesthesia Success., measured over 60 minutes per injection sequence..

The primary endpoint is the number of participants achieving pulpal anesthesia success. An electric pulp tester assessed lower-jaw molars, premolars, and incisors in four-minute time cycles over 60 minutes per injection sequence. Readings below 80 were classified as not numb, while a reading of 80 represented anesthetic success.

The registry’s success definition is more specific than simply recording a single reading at the maximum level. A participant had to reach the maximal device level of 80 by the fifth testing period, identified as 17 minutes after injection, and maintain that maximal response for the remainder of testing. The endpoint therefore converts repeated device assessments into a binary participant-level outcome: success or failure under that definition.

A binary endpoint is useful for answering a concrete question about how many participants met a stated success criterion. It also makes the comparison interpretable as a difference in the proportion of participants reaching the defined outcome. It does not preserve all the detail in the repeated readings, such as how readings changed over time or how close unsuccessful readings came to the threshold. Those features are not part of the posted primary outcome result.

The endpoint reflects the trial’s operational definition of pulpal anesthesia success, rather than every possible dimension of anesthetic experience. The registry record does not report additional primary measures of comfort, patient preference, or duration beyond the stated testing window.

7. Results Posted in the Registry

• Lidocaine + Lidocaine: 40.0% (40/100) versus 44.0% (44/100) on control; risk difference -4.0 percentage points (95% CI -17.7 to 9.7), risk ratio 0.91 (0.66–1.26); unadjusted two-proportion z-test p = 0.567.

8. Statistical Interpretation

9. Statistical Methods Explained

Why does the crossover structure matter?

In a parallel-group trial, each participant generally contributes an outcome to one assigned group. In this registry record, each participant received both injection sequences and served as their own control. The two binary outcomes from a participant are therefore paired. A participant’s result under one sequence may be related to their result under the other sequence, so an analysis that treats all observations as independent can fail to represent the study design.

Pairing can be informative because each participant is compared with themself, reducing the influence of stable differences between participants. But the analysis also depends on knowing how outcomes line up within participants. For binary outcomes, the important pattern includes participants who succeed under both sequences, participants who fail under both, and participants whose outcomes differ between sequences. The marginal success totals do not reveal that pattern.

What does McNemar’s test assess?

McNemar’s test is a method for comparing paired binary outcomes. Its comparison is informed by participants whose result differs between the paired conditions. Participants with the same result under both conditions do not contribute in the same way to the test of a difference. That is why the two group totals by themselves are not enough to reproduce the test statistic: the allocation of successes and failures within matched participants is needed.

The registry reports a McNemar analysis, a percentage difference of 0, and p = 1.00. The record does not post the paired outcome counts, the test statistic, a confidence interval, or additional details of the calculation. The sponsor’s reported result can therefore be quoted, but it cannot be independently reconstructed from the posted marginal counts.

What does the unadjusted recalculation add?

The simple recalculation uses the posted counts of 44 successes among 100 for mepivacaine plus lidocaine and 40 among 100 for lidocaine plus lidocaine. It reports a risk difference of -0.04 for the latter sequence relative to the former, an unadjusted p-value of 0.567, and a confidence interval that crosses zero. These calculations describe the contrast between the two marginal success proportions. They do not incorporate the participant-level pairing because that information is not included in the posted summary counts.

Risk difference is an absolute scale: it describes the difference between the proportions meeting the outcome. Relative risk compares those proportions as a ratio, while an odds ratio compares the odds of success. Each scale answers a slightly different descriptive question. In this crossover setting, marginal versions of these measures should be distinguished from a paired estimate that uses the participant-level response pattern.

How should a confidence interval and p-value be understood?

A confidence interval gives a range of effect values compatible with the observed data under the method’s assumptions. It communicates precision as well as direction: a wider interval reflects greater uncertainty, while an interval spanning zero for a difference is compatible with no difference. It does not mean that every value in the interval is equally likely, and it does not guarantee that the true effect lies inside that particular interval.

A p-value measures how unusual results at least as inconsistent with the null comparison would be under the null model and the assumptions of the test. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The sponsor’s p-value and the recalculated p-value arise from different approaches to the data, so they should be interpreted with attention to the paired design and the information used by each analysis.

What can and cannot be checked?

The registry gives the endpoint definition, counts, and sponsor-reported test, but does not report individual participant data or the paired success/failure cross-tabulation. It also does not report a confidence interval for the sponsor’s result. The unadjusted recalculation is therefore a useful check on the posted group totals, but it is not a reconstruction of the sponsor’s paired analysis.

General statistical methods can also be affected by issues such as over-dispersion, which occurs when observed variability exceeds what a model assumes. That concern is not established by this registry record, and no over-dispersion assessment is reported. More broadly, the record does not report the full statistical analysis plan, covariate adjustments, or procedures for assessing period or carryover effects. Those details should not be inferred from the fact that the trial used a crossover design.

10. Confidence Intervals and Precision

The recalculated risk difference is -0.04, with an interval that includes zero and extends in both directions. That interval indicates that the marginal-count estimate is not precise enough to distinguish no difference from differences favoring either sequence. The posted counts themselves are close, but the uncertainty matters: the observed contrast should not be treated as an exact or definitive estimate of the underlying difference.

For the crossover design, precision should ideally be assessed using the paired outcomes, because the relationship between each participant’s two results affects the variability of the comparison. The registry reports a McNemar p-value but does not report a confidence interval for the sponsor’s percentage difference. The paired-data precision therefore cannot be assessed from a posted interval for that analysis.

A confidence interval is not a range of possible observed counts. It is an uncertainty range for an effect estimate under the method used. If the interval for a difference spans zero, the data are compatible with no difference under that method, but may also be compatible with differences in either direction. An interval crossing zero does not prove equivalence, and an interval that is not statistically significant does not show that a meaningful difference is impossible.

The relative-risk and odds-ratio intervals are recalculations from the marginal counts and likewise should not be mistaken for paired estimates. The registry does not report confidence intervals for the sponsor’s analysis or a prespecified threshold for what would count as an important difference. Statistical precision and practical importance therefore cannot be fully connected using the registry record alone.

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 planning figures are participants per arm, not total events. They are illustrations based on the observed effect and are not the trial’s original sample-size justification. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario targets the stated fraction of the observed effect.

The 80% power column gives the approximate number of participants per arm for a future study to have an 80% chance of detecting the specified effect if that effect is present and the planning assumptions hold. The 90% power column gives the corresponding number per arm for a higher chance of detection under those assumptions. These are planning targets, not statements about what happened in this completed trial.

The rows describe planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The figures rise as the targeted effect becomes smaller: smaller effects are harder to distinguish from random variation, so more participants are needed to achieve the same planned power. For the full observed effect, the figures are 2,389 participants per arm for 80% power and 3,198 for 90% power. For 75% of the observed effect, they are 4,262 and 5,705; for 50%, they are 9,618 and 12,875.

These calculations are sample-size planning illustrations, not observed power. The trial enrolled 100 participants, and the registry record does not report the trial’s original design assumptions or its sample-size justification. The planning results should therefore not be used to claim that the completed study had a particular probability of finding a difference.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.440; treatment proportion p₁ = 0.400; average p̄ = 0.420.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6980 = 1.3680.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6974 = 0.5870.
4. n = (1.3680 + 0.5870)² / (-0.0400)² = 2,388.8, rounded up to 2,389 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
p0 <- 0.44                          # control proportion
p1 <- 0.4                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1574807)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 2,389 (80% power), 3,198 (90% power)
 75% of observed effect: n per arm = 4,262 (80% power), 5,705 (90% power)
 50% of observed effect: n per arm = 9,618 (80% power), 12,875 (90% power)
power.prop.test: 2388.8 
Simulated power at n = 2,389 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 registry reports the sponsor’s analysis as a McNemar test, with a percentage difference of 0 and p = 1.00. This is the analysis that reflects the paired structure described in the record, although the paired outcome counts and a confidence interval are not posted.

The unadjusted recalculation uses the marginal counts: 44 participants achieved success with mepivacaine plus lidocaine and 40 with lidocaine plus lidocaine, each among 100. It yields a risk difference of -0.04 and p = 0.567. Because it does not use the within-participant pattern, it is not a reproduction of the McNemar analysis. Its confidence interval spans zero, but no interval is reported for the sponsor’s result.

The two results should be distinguished rather than blended. The sponsor’s reported test addresses paired binary outcomes; the recalculation summarizes the difference between the posted marginal counts. The registry does not provide enough detail to reconcile the numerical difference between the analyses. Neither result, on its own, establishes equivalence or proves that a clinically important difference is absent.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure and one reported analysis, with no secondary outcomes posted. It does not report a multiplicity adjustment or describe a family of additional confirmatory tests. With only one posted primary outcome and one analysis, the record does not provide enough information to determine whether other analyses were planned or whether any multiplicity strategy was specified.

The record identifies the McNemar test and reports its result, but does not report the full statistical analysis plan, analysis population definitions, or handling of missing outcomes. It is therefore not reported in the registry record whether every enrolled participant contributed complete outcome data to both injection sequences, whether any participants were excluded from the analysis, or how missing testing results would have been treated.

The displayed counts of 100 for each sequence match the stated enrollment of 100, but that alone does not establish that all participants completed every assessment or clarify how incomplete measurements were handled. The paired outcome cross-tabulation is also not posted, so the individual-level pattern underlying the sponsor’s test cannot be inspected.

The registry record does not report an intention-to-treat definition, a per-protocol population, imputation procedures, sensitivity analyses for missing data, or adjustments for period and sequence. It also does not report whether subgroup analyses were planned. These omissions do not establish that such procedures were absent from the study; they mean that they are not reported in the registry record. In a crossover trial, clarity about completed periods and paired observations is particularly relevant because the analysis depends on outcomes from both conditions within participants.

15. Safety Results

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

Other (non-serious) adverse events

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

The registry lists 100 participants at risk for serious adverse events and 0 affected. It also lists 100 at risk for other adverse events and 0 affected. These are the posted figures for the treatment group. No serious adverse event terms are listed.

These counts describe what the registry record reports; they should not be interpreted as proof that no adverse events could occur or that the interventions are free of risk. The record does not provide further detail about event definitions, ascertainment procedures, severity categories beyond the serious-event grouping, or timing. Deaths are not reported in the registry record.

Because no affected participants are posted for either category, the record offers no event counts from which to compare event types or patterns. The safety figures should be read as registry-reported counts for this trial, not as a broad estimate of safety in other populations or settings.

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

The results describe a defined binary endpoint in a crossover trial: whether participants reached and maintained the electric pulp tester’s maximal reading according to the registry’s success rule. The posted counts are 44 of 100 for the mepivacaine-plus-lidocaine sequence and 40 of 100 for the lidocaine-plus-lidocaine sequence. The unadjusted marginal-count contrast is -0.04 for the latter relative to the former, with uncertainty that includes no difference.

The sponsor’s reported McNemar result is a percentage difference of 0 and p = 1.00. That test uses paired binary outcomes, consistent with each participant receiving both sequences. The registry does not provide the paired response counts or an interval for the sponsor’s estimate, so the reported paired result cannot be fully examined from the posted summary information. The unadjusted calculation is informative about the marginal counts, but it is not the same analysis.

These findings do not establish equivalence, noninferiority, or the absence of a meaningful difference. The registry does not report a prespecified margin for any of those conclusions. A nonsignificant result is not proof that the two sequences have identical outcomes. The uncertainty in the recalculated estimate also means that the observed count contrast should not be interpreted as a precise estimate of the difference expected in other settings.

The endpoint is based on the stated testing threshold and time course; it does not capture every aspect of anesthetic experience. The registry does not post secondary outcomes, broader patient-reported measures, or additional duration results. The findings should therefore be kept within the scope of the endpoint and study population described in the record, without turning them into medical advice or a general claim about treatment effects.

17. Why This Trial Matters Statistically

This trial is statistically useful because it illustrates why study design and analysis must be read together. The record describes a crossover in which each participant received both sequences, so the comparison is paired. Yet the most visible outcome counts are marginal totals, which do not show how each participant’s results correspond across the two sequences.

That distinction explains why an unadjusted recalculation from the group counts can differ from the sponsor’s McNemar result. The recalculation summarizes the difference between the two posted success proportions. McNemar’s test relies on within-participant discordance, information that cannot be recovered from those totals alone. Reporting paired counts and an interval for the paired effect would make the sponsor’s result more assessable.

The example also shows why a p-value is not a complete account of evidence. The sponsor’s p-value and the recalculated p-value are not interchangeable, and neither one alone describes the size and precision of the effect. The marginal recalculation includes an uncertainty interval spanning zero, while the registry does not post an interval for its paired result. Readers need to keep analysis choice, design, and precision in view together.

Finally, planning illustrations based on an observed effect should not be confused with the trial’s original design rationale. The registry gives enrollment but does not report its original sample-size assumptions. Separating post hoc planning scenarios from the completed trial’s design helps prevent misleading claims about power or what the study could reliably detect.

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.

The posted summary does not include the participant-level paired outcome pattern needed to verify or reproduce the McNemar analysis. It also lacks a confidence interval for the sponsor’s reported percentage difference. The recalculated marginal-count estimate and interval cannot replace those missing paired details.

The registry record does not report the analysis population, missing-data handling, crossover sequence details, washout procedures, or an assessment of period and carryover effects. These details are relevant to a crossover study, but their absence from the record is not evidence that the procedures were not performed.

The success endpoint depends on the specified device threshold and repeated testing rule. The registry provides no posted secondary outcomes, so the results cannot be extended to other measures of patient experience or to outcomes outside the defined endpoint. The record also does not report a prespecified threshold for a clinically important difference or an equivalence framework.

The sample-size planning figures are illustrations based on the observed effect and stated assumptions, not the trial’s original design plan. The original sample-size justification is not reported in the registry record. Finally, the safety listing records zero affected participants in the posted categories, but provides limited detail about ascertainment and event definitions. These constraints limit how much can be inferred beyond the reported counts and analyses.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Anesthetic Efficacy of 3% Mepivacaine Plus 2% Lidocaine With 1:100,000 Epinephrine for Lower Jaw Dental Injections — NCT01574807.
• Registry record last updated 2020-11-17; status last verified 2020-11.
• Results first posted 2020-11-17.
• 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

NCT01574807 is a completed Phase 4, randomized, double-blind crossover study sponsored by Ohio State University. It enrolled 100 participants and compared two sequences of lower-jaw dental injections. Each participant received both sequences and served as their own control.

The primary outcome was the number of participants achieving pulpal anesthesia success, defined by reaching and maintaining a maximal electric pulp tester response under the registry’s stated testing schedule. The registry posts 44 successes among 100 for mepivacaine plus lidocaine and 40 among 100 for lidocaine plus lidocaine.

The sponsor reports a McNemar test with a percentage difference of 0 and p = 1.00. An unadjusted recalculation from marginal counts gives a risk difference of -0.04 and p = 0.567, with an interval that includes zero. The paired outcome counts and confidence interval for the sponsor’s result are not reported in the registry record. The registry lists 0 serious adverse events and 0 other adverse events among 100 at risk in each category.