Pain Management in Teeth With Reversible Pulpitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pain Management in Teeth With Reversible Pulpitis (NCT07114198), a randomized early/phase 1 study. The primary outcome is Change in Pain Intensity From Baseline (Pre-Operative) to Immediately During the Procedure (Day 0), Measured by the Visual Analogue Scale (VAS).

2. Clinical Question

The registry describes a randomized controlled trial with a parallel-group design and single masking. Who was masked is not reported in the registry record. The central statistical question is about a between-group contrast in average change, not whether every child experienced the same response. The posted estimate and its confidence interval describe the observed group-level difference and the uncertainty around it; they do not establish the cause of that difference or its importance for an individual child.

3. Trial Design

The registry record describes NCT07114198, titled “Pain Management in Teeth With Reversible Pulpitis,” as a randomized, single-masked, parallel-group trial sponsored by Inonu University. Its listed phase is early phase 1. The record lists 46 participants enrolled and a completed status. The study start date is 2025-08-02, and the primary completion date is 2025-08-11.

Children in the ibuprofen group received a single oral dose of 10 mg/kg 40 minutes before vital pulp therapy. Children in the control group received no preoperative medication, and standard local anesthesia was administered before the procedure. The registry does not identify who was masked, describe the method used to generate or conceal the random allocation, or report further procedural details.

The primary outcome is mean change in pain intensity from preoperative baseline to immediately during the procedure, measured on the Visual Analogue Scale (VAS). The posted primary summaries include 22 participants in the control group and 22 in the ibuprofen group. The enrollment count and the group counts are both recorded; the registry does not explain the relationship between enrollment and the posted outcome counts.

One secondary endpoint is posted: change in VAS pain intensity from baseline to Day 1. The registry lists four outcome measures in total, but only one secondary result is included in the posted results. The number of analyses reported is zero, and no analysis plan, original sample-size justification, or explanation of the early-phase designation is reported in the registry record. This limits what can be learned about how the trial was planned and how its posted summaries were selected.

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: Randomization was performed using a sealed envelope method; the envelope contents were prepared by a third researcher before the examination. Because double-blinding was not possible, a single-blind design was employed. The clinician performing the procedure was aware of the groups, but the statistician performing the data analysis was unaware of the groups.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 7-13 years children

5. Baseline Characteristics

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

Population: All randomized participants who met the inclusion criteria and had baseline demographic data available were included in this analysis. One participant from each group was excluded due to protocol violation, leaving 22 participants per group (total n=44).

6. Primary Endpoint

The registry lists the primary outcome as Change in Pain Intensity From Baseline (Pre-Operative) to Immediately During the Procedure (Day 0), Measured by the Visual Analogue Scale (VAS), measured over Pre-Operative (Baseline) and Immediately During the Procedure (Day 0).

The primary endpoint is the change in pain intensity from preoperative baseline to immediately during vital pulp therapy on Day 0. Pain is measured using the VAS, described in the registry as ranging from 0 for no pain to 10 for the worst imaginable pain. The endpoint is a continuous score, summarized as a mean with a standard deviation. Its change score is defined as the score during the procedure minus the baseline score, with higher scores indicating worse pain.

A change measure focuses on how scores differ over the two assessment times rather than on the score at either time alone. Comparing average changes between randomized groups addresses whether their observed trajectories differed over this interval. The scale is intended to represent pain intensity, which is the outcome the trial description identifies as relevant during treatment.

Change scores also have interpretive limits. Their meaning depends on the starting scores and on how reliably pain was measured at each time. The registry does not report baseline group means, the individual-level relationship between baseline and procedure scores, or a threshold for a clinically important VAS change. The posted group summaries therefore describe average changes but do not show the range of individual experiences or establish what size of change would matter clinically.

7. Results Posted in the Registry

• Ibuprofen Group: mean 0.64 versus 5.05 on control; difference -4.41 (95% CI -5.95 to -2.87), standardized effect d = -1.69; z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change in Postoperative Pain Intensity From Baseline (Pre-Operative) to Day 1, Measured by the Visual Analogue Scale (VAS)

• 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:
  • Ibuprofen Group: mean 0.68 versus 0.59 on control; difference 0.09 (95% CI -0.73 to 0.91), standardized effect d = 0.07; z-test p = 0.829.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ibuprofen Group and the control. The interval gives the range of effects that remain compatible with the data.

One secondary endpoint is posted: change in VAS pain intensity from baseline to Day 1. Its group summaries and comparison are distinct from the primary measurement taken immediately during the procedure. In the Day 1 comparison, the estimated difference is close to zero relative to the interval’s range, and the interval includes values on both sides of zero. This contrasts with the primary result, whose interval lies below zero. The two outcomes therefore do not show the same degree of separation between the groups.

This difference across time points should not be read as a formal change in treatment effect over time. The registry does not report a repeated-measures analysis, a test comparing the contrasts across time, or a prespecified trajectory hypothesis. Each posted comparison addresses its own endpoint. The evidence for the primary question cannot be transferred automatically to the Day 1 question, and the later result does not negate the observed primary contrast.

The Day 1 result is secondary and its p-value is unadjusted. Secondary outcomes can help describe whether a primary pattern is accompanied by other findings, but they are often less definitive, particularly when multiple outcomes or time points are considered. Testing several outcomes increases the chance that at least one comparison may appear unusual even if there is no corresponding underlying difference. The registry does not report a multiplicity plan or a complete set of analyses, so the degree of selection or adjustment cannot be assessed.

The registry lists four outcome measures, while one secondary endpoint is posted in the results. The record does not explain whether other measures were collected, omitted, or not analyzed. Accordingly, the secondary evidence is best treated as limited context for the primary comparison, rather than as independent confirmation or a basis for a broad conclusion about outcomes over time.

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

• Change in Postoperative Pain Intensity From Baseline (Pre-Operative) to Day 1, Measured by the Visual Analogue Scale (VAS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant has a VAS change score, and the posted group summaries use the mean and standard deviation. A mean describes the arithmetic average of the observed scores within a group. A standard deviation describes how dispersed those scores are around that group’s mean. It is not the uncertainty in the mean itself; uncertainty in a mean also depends on the number of observations and the variability of the scores.

What does the mean difference represent?

The comparison is expressed as the ibuprofen-group mean minus the control-group mean. For the primary outcome, the estimate is -4.41 VAS points. A negative value means the average change was lower in the ibuprofen group under this subtraction order. The change-score definition is important: the endpoint subtracts baseline from the procedure score, so lower change means less increase in pain score, or a greater decrease, across those measurements. The estimate is an average contrast and does not indicate that all participants had the same change.

The comparison also reports a pooled standard deviation of 2.61 and a standardized effect estimate, d, of -1.69. Standardization expresses a mean contrast relative to a measure of variability, rather than in VAS points. Such a scale can help describe the size of a contrast relative to the spread of observed scores, but it does not replace the original-scale estimate or determine whether a difference is clinically important. The registry does not report a clinical-importance threshold.

How should the p-value be read?

A p-value describes how incompatible the observed result, or a more extreme result, would be with a specified null model. In the primary comparison the posted unadjusted p-value is <0.001. This is not the probability that the null hypothesis is true, the probability that the result occurred by chance, or a measure of the size or importance of the difference. Its interpretation depends on the assumptions and analysis used to calculate it. The statistical analysis procedure is not reported in the registry record, so the reported p-value should be read as the posted unadjusted result rather than as confirmation of a particular model specification.

For the secondary comparison the unadjusted p-value is 0.829. A large p-value does not prove that the groups have equal outcomes. It indicates that the observed comparison is not unusual under the null model used for that test. The confidence interval is useful alongside the p-value because it displays a range of plausible values for the difference and communicates the degree of precision in the original measurement scale.

Why does the confidence interval matter?

A confidence interval is a method for expressing uncertainty around an estimate. In repeated use under the assumptions of the method, intervals constructed in this way would contain the underlying parameter at the stated rate. For an individual trial, it is commonly read as a range of effect values compatible with the observed data and the analysis assumptions. It is not a range containing a specified proportion of individual participant outcomes.

For the primary result, both interval limits are negative. This indicates that the interval is on the lower-change side of zero for the ibuprofen-minus-control contrast. For the secondary result, the interval spans zero, so it includes no between-group difference as well as differences in either direction. The width of an interval matters: wider intervals reflect less precision than narrower ones, though precision alone does not establish clinical importance.

What does randomization contribute?

Random allocation is intended to make treatment groups comparable on average at the outset, including with respect to factors that may not have been measured. This supports interpretation of a between-group contrast as an effect of assigned group, provided the allocation and follow-up were implemented appropriately and the analysis respects the design. The registry identifies the allocation as randomized but does not report how randomization was generated or concealed, whether adherence was assessed, or which analysis population was used. Those details therefore cannot be evaluated from the registry record.

Single masking can reduce some forms of bias, depending on who is masked and how the outcome is assessed. The registry does not identify who was masked. Pain ratings are subjective measures, so the missing detail is relevant to judging how expectation or awareness might have influenced reporting. This observation is a general methodological consideration, not a claim that such influence occurred in this trial.

What assumptions underlie the planning illustrations?

The planning illustrations are based on the observed effect and are not the trial’s original design justification. Their stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The record does not report the trial’s original sample-size assumptions or explain whether the trial was designed around the primary endpoint.

These figures are prospective planning illustrations, not a retrospective measure of the quality of the trial. They depend on the observed effect, which can be unstable in a small study, and on the stated statistical assumptions. A different target effect or design assumption would produce different planning needs. The figures should therefore be read as conditional examples rather than as evidence that the trial was adequately or inadequately designed.

Because the analysis methods are not reported in the registry record, the descriptive summaries, mean differences, intervals, and p-values should not be taken as a complete account of data handling. The record does not state how missing observations, protocol deviations, or multiple outcomes were handled. These omissions constrain interpretation without changing the values posted for the comparisons.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the group difference, not whether the difference is important to patients. For the primary outcome, the estimated ibuprofen-minus-control mean difference is -4.41 VAS points. Its 95% confidence interval runs from -5.952 to -2.868. Every value in that interval is below zero, so the interval is consistent with a lower average change in the ibuprofen group under the stated subtraction order. The interval still allows a range of magnitudes, and it does not capture the range of individual children’s scores.

The primary group summaries are based on 22 participants in each arm. The control-group standard deviation is 3.51, while the ibuprofen-group standard deviation is 1.14. These describe variation among observed scores, not uncertainty in the group contrast. The reported confidence interval incorporates uncertainty in the estimated comparison; its width reflects both variability and the available sample information, together with the method used to construct it.

For the secondary Day 1 outcome, the mean difference is 0.09, with a 95% confidence interval from -0.726 to 0.905. Because this interval spans zero, the results are compatible with no difference and with differences in either direction over the range of the interval. This does not demonstrate equivalence. Establishing equivalence would require an appropriate prespecified margin and analysis, neither of which is reported in the registry record.

Confidence intervals rely on statistical assumptions, and the registry does not report the methods used to obtain them. They also do not account automatically for selection of outcomes or repeated testing. The reported intervals therefore help convey uncertainty around each comparison, but they do not resolve concerns about missing analysis details, multiplicity, or how well the participants represent children beyond this trial.

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, not as a total across both arms and not as total events. The registry states the planning assumptions: a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the listed fraction of the observed effect. These are planning illustrations based on the observed effect, not the trial’s original design assumptions, which are not reported in the registry record.

The 80% power column gives the number of participants per arm that the stated planning calculation associates with an 80% chance of detecting the specified effect if that effect is the true one and the assumptions hold. The 90% power column gives the corresponding number per arm for a 90% chance. These are design probabilities under assumed conditions; they are not probabilities that the observed result is true.

For the primary endpoint, planning for 100% of the observed effect gives 6 participants per arm for 80% power and 8 participants per arm for 90% power. Planning for 75% of the observed effect gives 10 and 14 participants per arm, respectively. Planning for 50% of the observed effect gives 22 and 30 participants per arm, respectively. Smaller target effects require more participants because a smaller contrast is harder to distinguish from random variation under otherwise similar assumptions.

For the Day 1 endpoint, the corresponding figures are much larger: planning for 100% of the observed effect gives 3,691 participants per arm for 80% power and 4,942 for 90% power; planning for 75% gives 6,562 and 8,785; and planning for 50% gives 14,764 and 19,765. These calculations are especially sensitive to the observed effect used as their starting point. The figures are not observed power and do not show the probability that the trial’s result is correct.

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 = -4.410; pooled standard deviation σ = 2.610.
2. n = 2 × (1.96 + 0.842)² × 2.610² / -4.410² = 5.5, rounded up to 6 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -4.41                      # observed difference in means
sigma <- 2.60956892991927                     # 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(7114198)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 6 (80% power), 8 (90% power)
 75% of observed effect: n per arm = 10 (80% power), 14 (90% power)
 50% of observed effect: n per arm = 22 (80% power), 30 (90% power)
power.t.test: 6.6 
Simulated power at n = 6 per arm: 0.749 (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

The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the primary and secondary outcomes. The primary endpoint is identified, and one secondary endpoint is posted, but the record lists four outcome measures in total. When several outcomes, time points, or analyses are examined, the chance of at least one apparently notable result can increase. Adjusting for multiplicity or specifying a hierarchy in advance can help control how the collection of tests is interpreted. Whether either approach was used in this trial is not reported in the registry record.

The posted p-values are explicitly unadjusted. They should therefore be interpreted as results for the individual comparisons, without assuming control of an overall error rate across outcomes. This matters especially when comparing a primary result with a secondary result: the secondary comparison can add descriptive context, but it is not automatically confirmatory evidence.

Missing-data procedures and the analysis population are not reported in the registry record. Although the record lists enrollment of 46 and gives outcome summaries for 22 participants in each group, it does not explain whether every enrolled participant contributed to each endpoint, whether any observations were missing, or how any missing values were handled. It also does not state whether analyses followed assigned groups, were limited to participants who completed treatment, or used another population definition. No explanation should be inferred from the counts alone.

Other relevant analysis details are not reported in the registry record, including the statistical model, covariate adjustment, handling of protocol deviations, and whether an analysis plan was finalized before results were examined. These omissions prevent a full assessment of the robustness of the estimates. They do not change the reported summaries, but they limit conclusions about how the results were generated and how completely they represent the planned analyses.

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 posted safety figures report zero serious adverse events among 22 participants at risk in the control group and zero among 22 participants at risk in the ibuprofen group. Deaths are reported as zero in both groups. The record also reports zero other adverse events in each group, with 22 at risk per group. No serious adverse-event terms are listed.

These are counts observed and reported for the groups, not evidence that the risk of an adverse event is zero. With a limited number of participants, uncommon events may not occur during the observation period even if they are possible. The registry does not report the duration or completeness of safety follow-up, how adverse events were collected, or whether the posted categories capture all events of interest. It also does not provide event-level descriptions because no serious terms are listed.

The figures should therefore be read narrowly: no serious or other adverse events and no deaths are recorded in these posted summaries. They do not establish comparative safety or exclude events that were not observed, collected, or reported. The registry record does not report further details needed to assess safety monitoring.

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

The posted primary result describes a lower mean change in VAS pain score during the procedure in the ibuprofen group than in the control group. The mean difference is -4.41 points, and its 95% confidence interval is from -5.952 to -2.868. The interval does not include zero, and the unadjusted p-value is <0.001. These statistics describe the observed comparison for this randomized trial and the uncertainty represented by the reported interval.

They do not show that every child experienced less pain, quantify an individual child’s response, or establish how important the mean difference is in clinical terms. The registry does not report a threshold for meaningful change on the VAS, and group averages can conceal different experiences among participants. Nor does the primary result settle the separate Day 1 question: the posted secondary comparison has a confidence interval that includes zero.

Randomization supports comparison of assigned groups, but assessing the strength of causal interpretation also requires information about allocation procedures, adherence, masking, follow-up, missing data, and analysis choices. Several of these details are not reported in the registry record. The registry identifies single masking but does not say who was masked. These gaps limit the ability to assess potential bias and generalizability.

The findings concern children aged 7–13 years undergoing vital pulp therapy for reversible pulpitis, under the described comparison of preoperative ibuprofen with no preoperative medication and standard local anesthesia. They should not be generalized automatically to other ages, conditions, procedures, doses, or settings. The posted result is statistical evidence about the observed trial contrast; it is not, by itself, a treatment recommendation or a complete account of benefits and harms.

17. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters. The primary outcome is not simply a pain score at one visit: it is the change from preoperative baseline to the time during the procedure. The direction of the mean difference can be understood only by combining the subtraction order with the scale interpretation. Here, the change is procedure score minus baseline score, and higher scores indicate worse pain.

It also illustrates the value of reporting an estimate with an interval, rather than relying only on a p-value. The primary mean difference is expressed in VAS points and accompanied by a confidence interval, allowing readers to consider both the direction and range of the observed contrast. The Day 1 comparison demonstrates a different inferential pattern: its interval includes zero and extends in both directions. The results emphasize that conclusions can differ by endpoint and measurement time.

The registry record also makes visible the distinction between posted outcome summaries and a fully described analysis. The trial is randomized, but important methods—including who was masked, how allocation was implemented, how missing values were handled, and what analysis population was used—are not reported. Such details help readers judge possible sources of bias and understand precisely what a comparison estimates.

Finally, planning figures based on observed effects are not substitutes for the trial’s original design rationale. They show how sample-size requirements change when the target effect is smaller, under stated assumptions, while leaving unanswered how the trial was originally planned. This is a useful statistical distinction when interpreting small clinical studies and their precision.

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 outcome summaries include 22 participants per group, while total enrollment is listed as 46. The registry record does not explain why the outcome counts do not match the enrollment count, whether all participants completed each assessment, or whether any data were unavailable. This leaves the completeness of outcome follow-up unclear.

The record identifies the trial as single-masked but does not state who was masked. This is particularly relevant to a subjective pain measure, though the registry does not establish that masking problems occurred. Allocation generation and concealment procedures, adherence, protocol deviations, and the analysis population are also not reported in the registry record.

Only one secondary endpoint result is posted even though four outcome measures are listed. The record does not explain the status of the other measures, whether analyses were prespecified, or how multiplicity was handled. The number of analyses reported is zero, and the statistical methods used to produce the posted comparisons are not described. These gaps make it difficult to assess selective reporting and the robustness of the inferences.

The trial has a limited enrollment, and the registry does not report a clinically important VAS threshold or the original sample-size justification. The planning illustrations rely on observed effects and stated assumptions, so they cannot establish whether the original design was adequate. The registry also does not provide detailed safety follow-up or describe the setting beyond the treatment context. These limitations constrain precision, transparency, and the extent to which results can be generalized beyond the participants and procedure described.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pain Management in Teeth With Reversible Pulpitis — NCT07114198.
• Registry record last updated 2025-09-24; status last verified 2025-08.
• Results first posted 2025-09-24.
• 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

NCT07114198 is a completed randomized, single-masked, parallel-group trial sponsored by Inonu University. The registry lists early phase 1 and enrollment of 46. It compares a single oral dose of ibuprofen, 10 mg/kg, 40 minutes before vital pulp therapy with no preoperative medication and standard local anesthesia in children aged 7–13 years with reversible pulpitis.

The primary endpoint is mean VAS pain change from baseline to immediately during the procedure. The posted ibuprofen-minus-control mean difference is -4.41, with a 95% confidence interval from -5.952 to -2.868 and an unadjusted p-value of <0.001. One secondary endpoint, pain change by Day 1, is also posted; its mean difference is 0.09, with a 95% confidence interval from -0.726 to 0.905 and an unadjusted p-value of 0.829.

Serious adverse events, other adverse events, and deaths are reported as zero in both groups. Important design and analysis details, including who was masked, missing-data handling, analysis populations, multiplicity procedures, and the original sample-size justification, are not reported in the registry record.