Analysis of Snore Sound Following Minimal Invasive Surgery in Sleep-disordered Breathing Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Analysis of Snore Sound Following Minimal Invasive Surgery in Sleep-disordered Breathing Patients (NCT01955083), a randomized na study. The primary outcome is Change in VAS Score After MIS.

2. Clinical Question

The central comparison is between two procedures, not between surgery and no intervention. The registry’s primary outcome is the mean change in VAS score at 3 months. Its analysis population consists of participants who completed the protocol, rather than everyone enrolled or assigned. This distinction matters when interpreting the estimates: the reported outcome reflects those with follow-up information, and the registry does not report outcomes for the two cases unavailable at follow-up.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. It lists an enrollment of 30 and two groups: Pillar implant surgery and radiofrequency surgery, each assigned 15 participants. The record is marked completed. The study dates recorded are 2010-08 for start and 2012-07 for primary completion. The phase is listed as not applicable.

The study’s brief description identifies participants with simple snoring or mild obstructive sleep apnea, a major complaint of snoring, and anatomy considered favorable for minimal invasive surgery. It describes collecting a validated Snore Outcome Survey and a visual analog measure of snoring, together with overnight objective snore-sound recording. The registry does not report the detailed eligibility criteria, allocation sequence generation, allocation concealment, or any procedures used to keep outcome assessment masked. Masking is recorded as none.

The primary analysis population was 28 protocol completers: 14 participants who underwent radiofrequency surgery and 14 who received a Pillar implant. The registry says two study cases were not available for follow-up. It does not report a separate intention-to-treat analysis or detailed reasons for missing follow-up. The primary outcome timeframe is baseline and 3 months following surgery. The record lists 13 outcome measures and 13 analyses, and lists 11 posted secondary outcomes.

Because both randomized groups received procedures, the between-group estimate addresses the relative difference between these two active approaches in the participants analyzed. It does not directly estimate either procedure’s effect against no surgery or against usual care. The registry’s designation of radiofrequency as the control group identifies the reference arm for comparisons; it does not make that arm an untreated control.

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: The additional inclusion criteria were: a) length of the soft palate ≥ 2.5 cm and b) the width of the base of the uvular ≥ 1.0 cm. The exclusion criteria were: a) tonsillar hypertrophy; b) high tongue position; c) retrognathia; d) craniofacial abnormalities, e) trismus, f) allergy to anesthetic, and g) poorly controlled medical disorders.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Twenty-eight patients completed the protocol; two study cases were not available for follow-up. Fourteen patients underwent radiofrequency surgery and 14 patients received pillar implant surgery. Accordingly, we analyzed the participants who completed the study protocol.

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 Change in VAS Score After MIS, measured over baseline and 3 months following surgery.

The primary endpoint is the mean change in subjective snoring severity, measured by VAS, at 3 months after minimal invasive surgery. The registry describes collecting the measure at baseline and at follow-up, so the endpoint focuses on change over that period rather than a single score at follow-up. The analysis includes participants who completed the protocol.

A subjective rating can capture how severe snoring is perceived to be, which is relevant to a study concerned with patients’ experience. The study description also explains that snoring can be evaluated instrumentally and that the investigators sought to explore the relationship between subjective perception and objective assessment. The VAS therefore represents one part of the study’s measurement approach; overnight sound recordings and questionnaire outcomes address related but distinct aspects.

The registry does not report the VAS scale’s range, its anchors, or the threshold for a change considered important to participants. Without those details, the size and direction of a numerical change should be described as a change in score, not assigned a clinical meaning beyond what the record states. The posted group means are negative, but the registry record does not describe the scale coding sufficiently to establish from these numbers alone how a negative score change should be interpreted. The endpoint is useful for comparing measured changes between the randomized groups, while its clinical interpretation depends on scale details and context not reported in the registry record.

7. Results Posted in the Registry

• Change in VAS Score at 3 Months After Pillar Implant: mean -3.30 versus -1.40 on control; difference -1.90 (95% CI -4.04 to 0.24), standardized effect d = -0.66; z-test p = 0.082.

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.

Percent Change in Total-SI After MIS

• 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 errors.
• Result:
  • Percent Change in Total-SI at 3 Months After Pillar Implant: mean -5.90 versus -48.90 on control; difference 43.00 (95% CI -23.29 to 109.29), standardized effect d = 0.48; z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Percent Change in Total-SI at 3 Months After Pillar Implant and the control. The interval gives the range of effects that remain compatible with the data.

Percent Change in Total-Imax After MIS

• 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 errors.
• Result:
  • Percent Change in Total-Imax at 3 Months After Pillar Implant: mean -6.80 versus 11.30 on control; difference -18.10 (95% CI -31.85 to -4.35), standardized effect d = -0.97; z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Percent Change in Total-Imax at 3 Months After Pillar Implant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent Change in Total-Imean After MIS

• 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 errors.
• Result:
  • Percent Change in Total-Imean at 3 Months After Pillar Implant: mean -0.40 versus 18.20 on control; difference -18.60 (95% CI -34.83 to -2.37), standardized effect d = -0.85; z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Percent Change in Total-Imean at 3 Months After Pillar Implant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists 11 posted secondary outcomes, covering questionnaire and acoustic measures. Numerical arm estimates and recalculated comparisons are recorded for several sound-characteristic outcomes. Across those recorded estimates, the direction is not uniform across measures: the results do not form a simple pattern in which every acoustic characteristic changes in parallel. This is a reminder that snore-sound recording captures multiple features rather than a single interchangeable measure of snoring.

These measures address related but distinct questions from the primary VAS endpoint. A subjective snoring rating concerns perceived severity, while instrumental sound measures characterize recorded sound. A difference in one type of outcome does not automatically establish a difference in the other, and the registry does not report a formal relationship between the primary subjective score and each acoustic measure. The study description identifies exploring that relationship as an aim, but the numerical results do not establish a general correlation on their own.

The secondary results can help describe the range of outcomes examined, but they should be interpreted alongside the primary comparison rather than as substitutes for it. No multiplicity adjustment is reported, and the registry does not give enough information to assess which secondary hypotheses, if any, were prioritized in advance. When many outcomes are examined, some estimates may appear notable due to chance variation. Unadjusted secondary findings consequently carry less evidential weight than a clearly prespecified primary analysis, and should be considered exploratory unless the registry record provides additional confirmatory context.

The secondary findings neither erase uncertainty in the primary VAS comparison nor independently settle the comparison between procedures. They instead show why subjective and objective measures need to be interpreted on their own scales, with attention to their distinct meanings and to the number of outcomes evaluated.

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

• Change in SOS Score After MIS
• Percent Change in Total-SI After MIS
• Percent Change in Total-Imax After MIS
• Percent Change in Total-Imean After MIS
• Percent Change in Total-Fpeak After MIS
• Percent Change in Total-Fmean After MIS
• Percent Change in B1-SI After MIS
• Percent Change in B1-Imax After MIS

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean change describe?

A change score compares a participant’s follow-up measure with their baseline measure. The group mean change is the average of those participant-level changes for the analyzed group. The between-group mean difference compares those group averages. In this registry’s recalculation, the contrast is expressed as the Pillar implant group minus the radiofrequency group. A negative value means the Pillar implant group’s numerical mean change is lower on that contrast; it does not, by itself, establish that the change is better or worse. That interpretation depends on the scale’s coding and context, which are not reported in the registry record.

General: a mean summarizes the arithmetic average and can be influenced by unusually high or low observations. It is not a description of every participant’s response. The registry record does not provide participant-level observations or a distribution of VAS changes, so the range of individual responses cannot be assessed from the posted means alone.

How should the confidence interval be read?

The primary change-score contrast is -1.9, with a 95% confidence interval from -4.04 to 0.240. General: a confidence interval expresses uncertainty around an estimated quantity under the assumptions of the method used. A wider interval represents less precision than a narrower interval on the same scale. An interval spanning zero is compatible with a range of values that includes no mean difference as well as values on either side of zero. It does not mean that every value in the interval is equally likely, and it does not measure the probability that a particular treatment effect is true.

The registry’s own reported interval uses a different stated analysis parameter: a mean difference in final values, estimated with a Wilcoxon (Mann-Whitney) method. It should not be substituted for the recalculated interval around a difference in mean changes. The registry does not describe the details needed to determine how its interval was constructed or why the reported test and interval have the stated relationship.

What does the unadjusted p-value tell the reader?

The recalculated comparison has an unadjusted p-value of 0.082. General: a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, nor does it give the probability that the result happened “by chance.” A p-value does not measure the size or clinical importance of an effect. Here it accompanies an estimated mean difference and its interval; those quantities together show the direction, magnitude, and uncertainty of the observed contrast.

“Unadjusted” means the stated p-value is not adjusted for the fact that multiple outcomes or comparisons may have been examined. The registry lists multiple outcomes, but the record does not report a multiplicity adjustment. This is one reason to give secondary p-values less weight than a single prespecified primary comparison.

Why is the sponsor’s method not the same calculation?

The registry reports a Wilcoxon (Mann-Whitney) analysis and identifies its parameter as a mean difference in final values. A Wilcoxon rank-sum procedure compares the distributions of ranks between groups; its test is not generally a direct test of a difference between arithmetic means. The registry’s reported parameter description and the named method therefore refer to different statistical summaries. The record does not provide further methodological details or a reconciliation with the baseline-to-follow-up mean change calculation.

General: rank-based methods can be useful when an analysis is intended to compare distributions without relying on the same assumptions as a direct comparison of means. Their interpretation depends on the distributional patterns in both groups, and should not automatically be paraphrased as a test of mean difference. The sponsor’s recorded result should be presented with its stated method, parameter, interval, and p-value rather than recast as the change-score estimate.

What do standard errors and secondary comparisons convey?

For the recorded secondary outcomes, arm-level dispersion is given as a standard error. General: a standard error describes the estimated uncertainty of a sample statistic, such as a group mean. It is not the spread of individual participant values; that is a different kind of variability. The registry’s secondary comparison estimates also have confidence intervals and unadjusted recalculated p-values. Those recalculations are simple, unadjusted comparisons derived from the posted summary statistics, and they do not replace the registry’s own reported analyses.

General: when measurements are numerous or correlated, examining each one separately can increase the chance of finding apparently notable results even when there is no corresponding pattern in the underlying effects. A prespecified analysis plan and a stated approach to multiplicity help readers understand how confirmatory the results are. The registry record does not report such details. Thus the secondary estimates are best treated as descriptive and exploratory rather than as a collection of independent confirmatory tests.

What can planning illustrations tell us?

The sample-size illustrations use the observed effect as a planning reference and vary the fraction of that effect to detect. General: planning calculations describe how many participants might be needed under specified assumptions to achieve a chosen probability of detecting an effect if that effect and those assumptions are correct. Such calculations depend on the effect size, variability, allocation, significance level, and statistical approximation. They do not establish the probability that the completed trial detected an effect, and they do not repair limitations in the observed data.

The registry record does not report the original design’s sample-size justification or assumptions. The posted planning assumptions are separate illustrations and should not be mistaken for the trial’s original protocol calculations. In particular, an illustration based on an effect estimated from this small completed sample is sensitive to how accurately that observed effect represents the effect that would be expected in a future study.

11. Confidence Intervals and Precision

The unadjusted recalculated primary contrast is -1.9, with a 95% confidence interval from -4.04 to 0.240. The interval crosses zero, encompassing both a negative and a positive mean difference under the stated contrast direction. The estimate is therefore not precise enough to isolate a single direction for the between-group difference. The interval also shows why the point estimate alone is incomplete: -1.9 is the center of the estimate, while the interval conveys substantial uncertainty around it.

Precision is affected by the amount of information in the analysis, the variability of the outcome, and the analysis method. Here, 14 participants per group completed the protocol and contributed to the primary analysis. The registry reports group-level variability and standard errors, but not participant-level data. The record also says two cases were not available for follow-up, and does not report their outcome values. Their absence means the completed-participant estimates do not directly describe all randomized participants.

The sponsor’s reported 95% confidence interval, from -14.4 to 48.4, concerns a stated mean difference in final values and accompanies a Wilcoxon (Mann-Whitney) analysis. It is not the same estimand as the recalculated interval for mean change. The two intervals should not be compared as though they were alternative estimates of exactly the same quantity.

General: greater precision means a narrower interval for the same estimand and method, but precision alone does not establish clinical importance or absence of bias. A narrow interval can still reflect limitations in study conduct or measurement, while a wide interval may leave a broad range of plausible effects. The registry does not report a threshold for a clinically important VAS difference, so the clinical importance of values within either interval cannot be determined from the record.

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 participants per arm, not total event counts. The registry’s planning 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. These are planning illustrations computed from the observed effect, not the original design assumptions for this trial; the original sample-size justification is not reported in the registry record.

In plain language, the 80% power column gives the illustrative number of participants per arm for a future design to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and those assumptions are correct. The 90% power column gives the corresponding per-arm number for a 90% chance. Those percentages describe design targets for a hypothetical study, not the probability that the current trial’s result is correct or that it has detected an effect.

The rows use the full observed effect, 75% of the observed effect, and 50% of the observed effect. As the assumed effect becomes smaller, more participants are required in the illustration to distinguish it from random variation under the same planning framework. The displayed values vary by outcome because the observed effect and variability differ. They are not a recommendation or a claim that the original trial was designed around those figures.

This is not observed power. Observed power calculated from the effect estimate after a study is complete largely restates the result and its uncertainty; the confidence interval and effect estimate are more informative descriptions of what the completed analysis found. The planning values instead show how hypothetical sample sizes change when the assumed effect size and target power change.

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 = -1.900; pooled standard deviation σ = 2.889.
2. n = 2 × (1.96 + 0.842)² × 2.889² / -1.900² = 36.3, rounded up to 37 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 <- -1.9                      # observed difference in means
sigma <- 2.88890771025345                     # 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(1955083)
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 = 37 (80% power), 49 (90% power)
 75% of observed effect: n per arm = 65 (80% power), 87 (90% power)
 50% of observed effect: n per arm = 146 (80% power), 195 (90% power)
power.t.test: 37.3 
Simulated power at n = 37 per arm: 0.799 (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. Analyses Reported by the Sponsor

The registry’s reported primary analysis uses a Wilcoxon (Mann-Whitney) method and describes the parameter as a mean difference in final values. It records a value of 17, a 95% confidence interval from -14.4 to 48.4, and p <0.05. The recalculated comparison is an unadjusted difference in mean changes from baseline: -1.9, with a 95% confidence interval from -4.04 to 0.240 and an unadjusted p-value of 0.082.

These results do not describe the same stated quantity: the registry analysis refers to final values, while the recalculation compares baseline-to-follow-up changes. The registry names a rank-based test, but describes its parameter as a mean difference. It does not report the detail needed to connect that test and interval to the change-score calculation. The record also reports a confidence interval spanning zero alongside p <0.05 for its own analysis; the basis for that combination is not explained in the registry record.

The two analyses should therefore be reported separately, with their methods and estimands identified. Neither the registry’s result nor the recalculation should be silently substituted for the other. The recalculation is an unadjusted reconstruction from posted summary statistics, while the registry’s analysis is the sponsor-reported result. The registry record does not provide an explanation resolving the differences.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 13 outcome measures and 13 analyses, and 11 posted secondary outcomes. The record does not report a multiplicity adjustment, a hierarchy of secondary endpoints, or a strategy for controlling the chance of false-positive findings across several tests. It is therefore not possible to determine from the registry record whether the secondary outcomes were intended to be confirmatory, exploratory, or organized in a prespecified testing sequence.

General: when multiple outcomes or comparisons are tested, the chance of at least one apparently unusual result can increase. Adjustment methods can address some forms of this problem, while prespecified ordering can clarify which tests are intended to support primary claims. Without a reported method, unadjusted secondary p-values should be interpreted cautiously. Their values do not by themselves show that a finding is robust to the full set of outcomes considered.

The primary analysis population is described as 28 protocol completers, with 14 participants in each group. The registry says two cases were unavailable for follow-up. It does not report their group-specific outcome data, detailed reasons for missingness, or whether missing outcomes were imputed. It also does not describe a separate analysis of all randomized participants. The effect of missing follow-up on the estimates cannot be evaluated from the recorded information alone.

General: an analysis limited to participants with observed follow-up can be biased if the probability of having an observed outcome is related to the outcome or to factors associated with it. The existence of missing data does not establish that such bias occurred, but it makes the missing-data process relevant to interpretation. The registry’s completed-participant analysis should therefore be understood as an analysis of observed protocol completers, with the impact of unavailable outcomes not quantified.

The record does not report a statistical analysis plan, detailed rules for handling protocol deviations, or whether the analysis population and methods were fixed before outcomes were examined. Those omissions limit assessment of prespecification and selective analysis, without establishing that such practices affected the results.

16. 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 3% reporting threshold.

The registry records 15 participants at risk for serious adverse events in the radiofrequency group and 15 in the Pillar implant group, with zero serious adverse events affecting participants in either group. It also records 15 participants at risk for other adverse events in each group, with zero other adverse events affecting participants in either group. The deaths field is not populated with a numerical result for either group, and the registry does not list serious adverse-event terms.

These entries should be read as the adverse-event counts recorded in the registry, not as proof that no adverse events of any kind occurred outside the record’s reporting scope. The number at risk for safety monitoring is 15 in each group, whereas the primary outcome analysis included 14 per group after two cases were unavailable for follow-up. The registry does not explain this difference in denominators or state whether the safety follow-up population differed from the primary analysis population.

General: zero recorded events in a small group provides limited information about the frequency of uncommon harms. The registry’s adverse-event entries do not establish comparative safety, and do not quantify the likelihood of events that were not observed or reported. The record does not provide detailed adverse-event definitions, surveillance procedures, severity grading beyond the serious/other categories, or the relevant observation period.

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

The posted results describe two procedures in a randomized comparison, with the primary analysis based on 28 participants who completed the protocol. The mean VAS changes were -1.4 for radiofrequency and -3.3 for a Pillar implant; the recalculated between-group difference in mean change was -1.9, with a 95% confidence interval from -4.04 to 0.240. These statistics describe the observed scores and the uncertainty in their between-group contrast. They do not, without further scale information, identify the clinical meaning of the negative score changes.

The interval includes zero, so the recalculated data are compatible with a range of between-group mean differences rather than a single clearly separated value. That is not evidence that the procedures are identical, and it is not proof of a difference. The estimate’s uncertainty, the small completed-participant analysis, and the unavailable follow-up cases all matter when considering what can be inferred.

The registry’s own reported analysis is different in its stated parameter and method from the unadjusted change-score recalculation. Its final-value mean-difference description, rank-based method, reported interval, and p-value should be considered as recorded, without treating it as the same estimate as the primary change-score contrast. The record does not explain their relationship.

The secondary acoustic measurements add descriptive information, but their interpretation is limited by multiple outcomes and the absence of reported multiplicity handling. The record does not establish a general correlation between subjective ratings and objective sound measures. Nor does it show how either procedure compares with no surgery, how results persist beyond the stated follow-up, or whether observed score changes are important to participants. The results are therefore specific to the outcomes, analysis population, comparison, and follow-up recorded.

Nothing in these findings should be read as individualized medical guidance. They are statistical descriptions of this trial’s recorded outcomes, not a determination of what option an individual should choose.

18. Why This Trial Matters Statistically

This trial raises a useful measurement question in clinical research: subjective reports and instrumentally recorded sounds may capture related, but not identical, aspects of snoring. Measuring both can help researchers distinguish perceived severity from features of an overnight sound recording. Their relationship needs to be evaluated directly rather than assumed, and the registry’s study aims reflect that distinction.

Statistically, the comparison also illustrates why the outcome definition and estimand matter. A mean change from baseline is not the same quantity as a difference in final values. The registry’s own analysis and the unadjusted recalculation are therefore not interchangeable, even though both concern the same groups and primary outcome area. Clear reporting of the outcome, analysis population, contrast, and method is essential for readers to understand what an estimate represents.

The small number of completers also makes uncertainty especially important. Reporting an estimate alongside its confidence interval gives readers more context than relying on a point estimate or thresholded p-value alone. The interval for the recalculated primary contrast includes zero and permits a range of values; the record does not provide a clinically important threshold that would connect that range to practical relevance.

Finally, the trial highlights the role of transparent reporting. Information about missing follow-up, multiplicity, the original sample-size rationale, scale coding, and the statistical analysis plan would help readers assess how much confidence to place in primary and secondary findings. These are general reporting considerations; the registry record does not contain those details. Their absence limits interpretation without establishing that a particular analysis choice was inappropriate.

19. 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 primary analysis includes 28 protocol completers rather than all 30 enrolled participants. The record reports that two cases were unavailable for follow-up but does not give their group assignments, reasons for missingness, or outcomes. No missing-data analysis is described. This limits assessment of whether the completer results represent all randomized participants.

The registry does not describe the VAS range, anchors, or direction of coding, or a threshold for an important change. The numerical score changes can therefore be reported, but their clinical interpretation is constrained. The study’s eligibility description refers to simple snoring or mild obstructive sleep apnea and favorable anatomy, but detailed criteria are not reported in the registry record. The applicability of the results beyond the described participants is consequently difficult to judge.

The trial is recorded as unmasked, and the primary endpoint is subjective. The registry does not describe masked outcome assessment or procedures to limit expectation-related influences on subjective scoring. This does not establish that such influences affected the results, but it is relevant context for interpreting a subjective outcome in an unmasked study.

The sponsor-reported analysis and the recalculated change-score analysis concern different stated quantities and methods, and the registry does not reconcile them. The record also does not report a multiplicity strategy despite several outcomes, or the original sample-size justification and assumptions. Further, the primary endpoint is evaluated at 3 months; longer-term outcomes are not described in the primary timeframe. The registry’s adverse-event entries report zero events in the listed categories, but do not give detailed surveillance methods or event definitions. Together, these limitations constrain interpretation of precision, clinical importance, generalizability, and the consistency of the recorded statistical analyses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Analysis of Snore Sound Following Minimal Invasive Surgery in Sleep-disordered Breathing Patients — NCT01955083.
• Registry record last updated 2014-08-18; status last verified 2013-10.
• Results first posted 2014-08-18.
• 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.

23. Record Summary

NCT01955083 is a completed randomized, parallel-group trial comparing Pillar implant surgery with radiofrequency surgery for participants with primary snoring or obstructive sleep apnea. The registry lists an enrollment of 30, no masking, and 15 participants assigned to each procedure. The primary outcome is mean change in VAS snoring severity at 3 months following surgery.

The primary analysis includes 28 protocol completers, 14 per group; two cases were unavailable for follow-up. The recalculated mean difference in change is -1.9, with a 95% confidence interval from -4.04 to 0.240 and unadjusted p = 0.082. The registry separately reports a Wilcoxon (Mann-Whitney) analysis of final values. Its relationship to the change-score calculation is not explained. Multiple secondary outcomes are listed, with no multiplicity method reported. Safety entries record zero serious and zero other adverse events in each group.