Buspirone for Functional Dysphagia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Buspirone for Functional Dysphagia (NCT02674412), a randomized na study. The primary outcome is Change in Distal Contractile Index (DCI) on High Resolution Esophageal Manometry.

2. Clinical Question

The clinical question is whether the recorded swallowing-related measure changed differently during buspirone and placebo periods. Because participants were assigned to sequences and were to receive both treatments, the design can, in principle, compare treatment periods within the same people. Such comparisons may account for stable differences between participants, but they need an analysis that respects the repeated observations and the sequence of treatments. The registry record does not report a sponsor analysis or enough detail to determine how the posted group summaries were constructed or how within-participant information was handled.

3. Trial Design

The registry record describes a randomized, quadruple-masked, crossover-style study sponsored by The Cleveland Clinic. The status is completed, and enrollment is listed as 10. The record gives a start date of 2016-02 and a primary completion date of 2017-04-12. Phase is listed as NA. These details describe the registered study; they do not establish which participants contributed data to each outcome or whether all scheduled treatment periods were completed.

The two listed sequences were buspirone then placebo and placebo then buspirone. The buspirone period is described as 10 mg by mouth three times daily for two weeks, followed by a two-week washout and two weeks of placebo. In the opposite sequence, placebo was given three times daily for two weeks, followed by a two-week washout and two weeks of buspirone 10 mg three times daily. The registry summary also describes random assignment to the first treatment, followed by the other treatment after washout.

A crossover design differs from a parallel-group design because participants are intended to receive both treatments over time. The same person may therefore contribute observations under buspirone and placebo. The sequence matters: treatment effects can be difficult to distinguish from period effects or residual effects of an earlier treatment if these are not addressed. The registry record does not report the crossover-specific statistical model, handling of period or sequence effects, or assessment of carryover. It also does not report the original sample-size justification, interim analyses, or the trial's planned statistical analysis in sufficient detail to assess these design features.

There are two listed secondary outcomes: change in a gastroesophageal reflux disease health-related quality questionnaire score and change in the percentage of normal swallows in a series of 10 measured swallows. The record lists three outcome measures in total, while no sponsor-reported analyses are listed. Consequently, the available comparisons are best read as descriptive and unadjusted, rather than as a complete account of a prespecified crossover analysis.

4. Participant Flow and Accounting

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

Overall Study

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: Analysis was performed for each subject during two separate periods--once while on Buspirone and once while on Placebo.

6. Primary Endpoint

The registry lists the primary outcome as Change in Distal Contractile Index (DCI) on High Resolution Esophageal Manometry, measured over Change in the score from Baseline to 14 days.

The primary endpoint is change in distal contractile index, or DCI, on high-resolution esophageal manometry. DCI measures the strength of esophageal muscle contractions during swallowing and is expressed in mm Hg. The registry description says values greater than 450mm Hg are considered normal. The recorded timeframe is change from baseline to 14 days.

Manometry offers a quantitative measure of contraction strength, so it can capture a physiologic feature related to swallowing rather than relying only on a participant's description of symptoms. That makes it relevant to a study of functional dysphagia, but it is not itself a complete measure of swallowing experience, daily function, or quality of life. The registry record does not specify how a change in DCI should be interpreted in relation to patient-perceived improvement or what magnitude of change would be clinically meaningful.

The posted DCI values are mean changes with standard deviations. The treatment contrast is a difference between the buspirone and placebo means, accompanied by a confidence interval. Those summaries describe group-level changes and their variability; they do not show how each participant's value changed, whether all participants completed both periods, or how measurements from the same participant were linked across treatment conditions. A crossover-aware analysis could use that pairing, but the analysis method is not reported in the registry record.

7. Results Posted in the Registry

• Buspirone: mean 241.90 versus 340.40 on control; difference -98.50 (95% CI -770.54 to 573.54), standardized effect d = -0.13; z-test p = 0.774.

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 Gastroesophageal Reflux Disease - Health Related Quality Questionnaire Score

• 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:
  • Buspirone: mean -4.10 versus -10.20 on control; difference 6.10 (95% CI -11.08 to 23.28), standardized effect d = 0.31; z-test p = 0.487.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Buspirone and the control. The interval gives the range of effects that remain compatible with the data.

Change in Percentage of Normal Swallows Recorded in a Series of 10 Measured Swallows.

• 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:
  • Buspirone: mean 15.00 versus 20.00 on control; difference -5.00 (95% CI -38.32 to 28.32), standardized effect d = -0.13; z-test p = 0.769.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Buspirone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints cover a patient-reported health-related quality questionnaire and a manometry-based measure of normal swallows. Across these outcomes and the primary DCI measure, the posted mean contrasts do not form a consistent pattern pointing uniformly in one direction. The secondary estimates are uncertain, and their confidence intervals span differences in either direction. Taken together, they do not provide a clear independent resolution of the uncertainty in the primary result.

These outcomes address related but distinct aspects of dysphagia and swallowing. Agreement across measures might strengthen a coherent interpretation, while disagreement can arise because the measures capture different constructs, have different variability, or are imprecisely estimated. In this record, the small enrollment and broad variation make it difficult to distinguish meaningful consistency from random fluctuation. The results should not be treated as proof that one endpoint validates another.

Each secondary comparison is unadjusted, and no sponsor-reported analyses are listed. When multiple outcomes are considered, the chance of obtaining a seemingly notable result by chance can increase unless the analysis accounts for multiplicity. The registry record does not report a multiplicity strategy or identify confirmatory versus exploratory outcomes beyond naming the primary and secondary measures. The secondary findings therefore carry less weight than a prespecified, adequately powered primary analysis and should be interpreted as exploratory. They do not alter the main conclusion that the primary contrast is imprecise and that the registry does not report the trial's own analysis.

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

• Change in Gastroesophageal Reflux Disease - Health Related Quality Questionnaire Score
• Change in Percentage of Normal Swallows Recorded in a Series of 10 Measured Swallows.

9. Statistical Interpretation

10. Statistical Methods Explained

The statistical summaries describe continuous outcomes using means and standard deviations. A mean is the arithmetic average of the observed values in a group. A standard deviation describes how dispersed individual observations are around that average; it is not the uncertainty of the mean itself. When observations vary greatly, a mean may be estimated less precisely, particularly when the sample is small.

What does the mean difference represent?

The primary contrast is the buspirone mean minus the placebo mean. A negative estimate means the posted buspirone mean is lower than the posted placebo mean; a positive estimate would mean it is higher. This direction alone does not determine clinical importance, because the registry record does not give a clinically meaningful threshold for DCI change. The contrast is an unadjusted recalculation from the reported group summaries, not a substitute for a sponsor-reported analysis.

The recalculated comparison uses the group means and variability to estimate a difference and its uncertainty. Such a calculation is straightforward for independent groups, but the registered design is crossover-style: participants were scheduled to receive both treatments. Within a participant, outcomes under the two conditions may be correlated. A comparison that ignores that correlation may not use the design's information in the same way as a paired or otherwise crossover-aware analysis. The registry record does not report a sponsor analysis, so the posted summary statistics cannot establish whether such an analysis was performed elsewhere.

How should the confidence interval be read?

A confidence interval gives a range of values that are compatible with the estimate under the assumptions of the calculation. It conveys uncertainty around the difference rather than a guarantee that the true effect lies in the interval. A narrow interval indicates greater precision; a broad interval indicates less precision. For the primary contrast, the interval extends from -770.5 to 573.5 mm Hg. Because the range covers both directions and includes no difference, it does not pin down the direction or size of the contrast.

The interval's interpretation depends on the method used to calculate it. If the calculation does not account for repeated measurements or other crossover features, its uncertainty may not correspond to the uncertainty from an appropriate crossover analysis. The registry record does not identify the model or adjustment procedure used for a sponsor analysis, nor does it report participant-level data needed to reconstruct one.

What does the p-value say?

The unadjusted p-value is a measure of how compatible the observed contrast is with a specified null model of no treatment difference, assuming the model's conditions hold. It is not the probability that the null hypothesis is true, and it does not measure the probability that a finding is due to chance. The primary p-value is 0.774. On its own, it does not establish that the treatments have the same effect. It should be interpreted alongside the estimate, confidence interval, sample size, variability, and design.

Multiplicity is relevant because more than one outcome is reported. Testing several outcomes can increase the chance of at least one apparently notable result arising by chance when each is considered separately. The secondary comparisons are unadjusted, and no multiplicity procedure is reported in the registry record. They should therefore be treated as exploratory rather than as independent confirmatory evidence.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a model would expect under its assumptions. For a continuous outcome, large spread relative to the mean contrast makes the estimate less precise and can make it harder to distinguish a treatment difference from random variation. The posted primary standard deviations are 771.7 mm Hg and 761.7 mm Hg, while the estimated mean difference is -98.5 mm Hg. These summaries indicate that the observed spread is large in relation to the contrast, although they do not reveal the distribution of individual observations or identify why that variability occurred.

High variability can reflect genuine differences among participants, measurement variability, unusual observations, or other sources. Those are general possibilities, not findings established by this registry record. Individual data and diagnostic summaries are not reported in the registry record, so the source and pattern of the spread cannot be assessed.

What is not established by the registry summaries?

The record does not report the sponsor's analysis results, a crossover-specific model, analysis populations, missing-data methods, or details about protocol deviations. It also does not report the trial's original sample-size justification or whether interim analyses were planned or conducted. Those omissions limit assessment of whether the posted summaries align with the study's prespecified analysis. The simple recalculated comparisons are useful descriptive checks, but they should not be mistaken for a complete analysis of a randomized crossover trial.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate the treatment contrast. The primary estimate is -98.5 mm Hg, while its 95% confidence interval runs from -770.5 to 573.5 mm Hg. This is a broad interval that allows the observed contrast to be compatible with substantially lower or higher mean change under buspirone relative to placebo. It includes no difference, so the data do not identify a clear direction of the primary contrast.

The interval should not be read as proof that all values within it are equally plausible, nor as a range guaranteed to contain the true effect. It summarizes uncertainty under the calculation's assumptions. Those assumptions matter in this study because the design is crossover-style, while the available calculation is an unadjusted comparison of group summaries. The registry record does not report whether the trial's own analysis accounted for paired measurements, treatment period, sequence, or carryover.

The primary group standard deviations, 771.7 mm Hg and 761.7 mm Hg, are large, and the enrollment is 10. The combination of broad variability and limited enrollment is consistent with the wide uncertainty, although the registry summaries cannot isolate the contribution of each factor. No clinically meaningful difference threshold is reported, so the interval cannot be classified as excluding or confirming a clinically important effect. The posted data support an imprecise estimate, not a precise conclusion of no effect.

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 sample-size figures are planning illustrations based on the observed effect, not a record of the trial's original design justification. They give participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: these are continuous outcomes, and the stated unit is participants per arm. The trial's own original sample-size assumptions are not reported in the registry record.

The illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The rows describe planning for 100%, 75%, and 50% of the observed effect. Under each effect assumption, the 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting an effect of that size under the planning assumptions, if that effect exists. The 90% power column uses a higher target chance of detection and therefore requires more participants per arm.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. The figures are hypothetical planning scenarios and are sensitive to the observed effect and variability in this small trial. They are not a recommendation, a reconstruction of the original protocol, or observed power. Observed power is not an appropriate way to interpret the trial's result; the estimate and its confidence interval convey the uncertainty in the posted comparison more directly.

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 = -98.500; pooled standard deviation σ = 766.716.
2. n = 2 × (1.96 + 0.842)² × 766.716² / -98.500² = 951.1, rounded up to 952 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 <- -98.5                      # observed difference in means
sigma <- 766.71630346563                     # 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(2674412)
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 = 952 (80% power), 1,274 (90% power)
 75% of observed effect: n per arm = 1,691 (80% power), 2,264 (90% power)
 50% of observed effect: n per arm = 3,805 (80% power), 5,094 (90% power)
power.t.test: 952.1 
Simulated power at n = 952 per arm: 0.797 (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 identifies a primary outcome and two secondary outcomes, but it does not report a multiplicity adjustment or a hierarchy for interpreting the secondary outcomes. In general, testing several outcomes creates more opportunities for a result to appear notable by chance. Unadjusted secondary p-values should therefore be read cautiously and should not be treated as confirmatory evidence without a prespecified analysis plan. The registry record does not say whether a multiplicity plan was specified or used.

Missing-data handling is not reported in the registry record. The record lists enrollment as 10 and gives summary sample sizes of 10 for each treatment condition, but these figures alone do not describe completeness of each participant's observations across both crossover periods, reasons for missing measurements, or how incomplete sequences were handled. No imputation method, complete-case rule, or sensitivity analysis is reported. It is therefore not possible to determine whether missingness could have affected the estimates.

Analysis populations are also not reported in the registry record. The available summaries do not establish whether the reported outcomes include all randomized participants, only those who completed both periods, or another defined set. The record does not describe adherence, protocol deviations, or exclusion criteria for the analysis. These details matter because exclusions after randomization can change the comparability created by random assignment.

The record lists no sponsor-reported analyses. It also does not report a crossover-specific method, or how period, sequence, within-participant correlation, or possible carryover were addressed. Consequently, the recalculated unadjusted comparisons should not be presented as the definitive analysis of the trial. The absence of these details is a limitation of the registry record; it does not establish that the trial team did not perform analyses or manage missing data in another setting.

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 5% reporting threshold.

The registry safety summaries list 10 participants at risk in each treatment group. For buspirone and placebo, the reported counts affected by serious adverse events are 0, the counts affected by other adverse events are 0, and deaths are 0. No serious adverse-event terms are listed. These are the events recorded in the posted summaries, not proof that no symptoms or events occurred outside the reported categories.

Zero reported events in a small study provides limited information about uncommon harms. The figures do not show the duration of safety follow-up, severity or timing of non-serious symptoms, or whether events were assessed in a crossover-specific way. The registry record does not report additional detail on safety definitions, attribution, or exposure time. These summaries should be read as a record of what was reported, rather than as a comprehensive estimate of safety.

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

The posted results describe mean changes in DCI under buspirone and placebo, with an unadjusted recalculated difference of -98.5 mm Hg. The confidence interval is broad and crosses no difference, and the unadjusted p-value is 0.774. These findings do not establish a clear treatment contrast. They also do not demonstrate that buspirone and placebo are equivalent, because the record gives no equivalence margin and the interval allows a wide range of effects.

The result is specific to the registered population, outcome, and short measurement timeframe. The primary measure is a physiologic measure of esophageal contraction strength, not a direct summary of all symptoms or functioning. The record does not identify a minimum clinically meaningful change, and it does not explain how a change in DCI relates to a participant's experience of dysphagia. The secondary outcomes add information about other measures, but they are also unadjusted and imprecise.

The crossover design could make within-person comparisons informative, but the registry record does not report the sponsor's model or results. The available recalculated comparison is unadjusted and cannot establish that period, sequence, or carryover effects were considered. The absence of a reported analysis, missing-data approach, and analysis population further limits interpretation.

Thus, the registry results should be understood as uncertain descriptive evidence rather than a definitive estimate of treatment effect. They do not support a claim that buspirone works or does not work, and they do not justify a medical decision. A larger, fully reported analysis with appropriate crossover methods and clear patient-relevant interpretation would be needed to resolve the statistical uncertainty.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate and a p-value are not enough to understand a clinical comparison. The primary mean difference is modest relative to the observed spread, and its confidence interval is broad. Looking at the interval makes the uncertainty visible: the posted data are compatible with contrasts in either direction rather than concentrating around one precise effect.

The crossover design also illustrates that the statistical structure of a study matters. Participants were assigned to sequences and were intended to receive both treatments. In that setting, observations from the same person are related, and a suitable analysis needs to reflect that relationship and the timing of treatment periods. A simple unadjusted comparison of summary means does not show whether those features have been accounted for. Without the sponsor's reported analysis, readers cannot evaluate how the trial's design was used statistically.

The registry also demonstrates the difference between planning illustrations and the study's actual design rationale. The planning figures use an observed effect and stated assumptions; they cannot be interpreted as the original sample-size justification or as evidence of observed power. This distinction matters especially when the observed estimate is imprecise and the enrollment is small.

Finally, multiple outcomes and incomplete reporting affect how much confidence can be placed in any single result. Without a reported multiplicity plan, missing-data approach, analysis population, or crossover model, the secondary findings are best treated as exploratory. Transparent reporting of these methods would help readers distinguish a genuinely informative null result from a study that cannot resolve the question precisely.

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 enrollment of 10 limits the amount of information available, while the primary standard deviations are large. The resulting primary confidence interval is wide. The registry record does not report participant-level data, outcome distributions, or diagnostics, so it is not possible to assess skewness, influential observations, or whether the mean adequately represents the observations.

The crossover structure creates additional interpretive questions. The treatment sequences and washout are described, but the registry record does not report the crossover analysis, within-participant correlation, period effects, sequence effects, or assessment of carryover. The posted comparison is a simple unadjusted recalculation from group summaries; it may not capture all the information or assumptions relevant to a crossover analysis.

The registry does not report a clinically meaningful threshold for DCI change, the original sample-size justification, analysis populations, handling of missing observations, protocol deviations, or a multiplicity strategy. No sponsor-reported analyses are listed. These gaps prevent assessment of whether the reported summaries were prespecified, whether all randomized participants were included, or how uncertainty was handled in the trial's own analysis.

The study's registered outcome timeframe is short, and the primary endpoint is physiologic rather than a direct report of swallowing symptoms or daily impact. The record does not provide enough information to relate changes in DCI to changes that participants would experience as meaningful. These limitations concern interpretation of the registry record and do not imply that unreported methods or data were not available to the investigators.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Buspirone for Functional Dysphagia — NCT02674412.
• Registry record last updated 2018-08-10; status last verified 2018-06.
• Results first posted 2018-08-10.
• 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

NCT02674412 is a completed randomized, quadruple-masked, crossover-style study of buspirone and placebo for functional dysphagia, sponsored by The Cleveland Clinic. Enrollment is listed as 10. The primary endpoint is change in DCI from baseline to 14 days, measured by high-resolution esophageal manometry.

The unadjusted recalculated primary mean difference is -98.5 mm Hg, with a 95% confidence interval from -770.5 to 573.5 mm Hg and p = 0.774. The estimate is imprecise, and the registry record lists no sponsor-reported analyses. The record also includes two secondary outcomes and reports zero serious adverse events, zero other adverse events, and zero deaths in each treatment summary. Missing-data methods, analysis populations, multiplicity handling, and the crossover-specific analysis are not reported in the registry record.