Reversing Synchronized Brain Circuits With Targeted Auditory-Somatosensory Stimulation to Treat Phantom Percepts: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Reversing Synchronized Brain Circuits With Targeted Auditory-Somatosensory Stimulation to Treat Phantom Percepts (NCT03621735), a randomized na study. The primary outcome is Change in Objective Tinnitus Loudness.

2. Clinical Question

3. Trial Design

This completed study, NCT03621735, is a randomized, quadruple-masked crossover trial sponsored by the University of Michigan. The registry lists the phase as NA. In a crossover design, participants receive more than one treatment condition over time. Here, participants were assigned to receive both active stimulation and sham stimulation, with the order randomized. The arm descriptions identify a sham-then-active sequence and an active-then-sham sequence. They state that participants were blinded to which treatment they were receiving.

The brief summary describes a washout period of 6 weeks after each arm and an expected participation period of approximately 36 weeks. The primary outcome description reports measurements weekly during each treatment arm and washout, with results presented in six-week intervals through the stated timeframe of up to 24 weeks. The reported categories distinguish the first treatment period, its washout, the second treatment period, and its washout for each sequence. The record describes repeated representation of participants across trial segments to assess possible spillover effects. Consequently, the counts for segments should not be read as separate groups of unique people.

The registry reports enrollment of 100, while the brief summary says the study would enroll up to 300 individuals. These are different statements about enrollment and intended recruitment; the record does not explain the difference. The study is marked completed. Its start is listed as 2018-11-01, and primary completion as 2022-07-06.

The intervention descriptions identify active and sham bimodal auditory-somatosensory stimulation delivered using a take-home device. The intervention labels elsewhere in the record use Burst-SCS/sham SCS terminology; a reconciliation of those labels with the arm descriptions is not reported in the registry record. The original statistical analysis plan, including any prespecified model for crossover or period effects, is not reported in the registry record.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Because of the crossover nature of this trial, and to determine whether spillover effects were present, participants are represented multiple times for each segment of the trial in which they participated.

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 Objective Tinnitus Loudness, measured over Up to 24 weeks.

The primary endpoint is change in objective tinnitus loudness, measured with TinnTester and expressed in decibels sensation level (dB SL). The registry describes a self-directed computerized assessment that estimates how loud participants perceive their tinnitus to be. Weekly assessments were collected during treatment and washout periods. The outcome description says absolute differences were averaged relative to baseline to determine loudness change.

This measure gives a continuous numerical summary rather than sorting participants into categories. A mean describes the average reported change for a group or trial segment. The registry posts means and standard errors for the sequence-specific periods. The negative means indicate changes below the baseline reference as represented in the posted outcome summaries; they should not be interpreted as a comparison of active treatment against sham by themselves. The order and timing of each period matter because participants crossed between conditions, and the record explicitly notes concern about possible spillover.

The endpoint is useful for describing change in a measured tinnitus-loudness estimate across the trial schedule. It does not, on its own, establish whether a difference is important to participants or whether it is attributable to active stimulation rather than period, sequence, carryover, or other influences. A threshold for clinically important change is not reported in the registry record. Nor does the record post a sponsor-reported inferential analysis for this outcome. Interpretation therefore rests on the posted descriptive summaries and the unadjusted comparisons, with their uncertainty kept in view.

7. Results Posted in the Registry

• Active First: mean -6.10 versus -10.20 on control; difference 4.10 (95% CI -1.62 to 9.82), standardized effect d = 0.32; z-test p = 0.160.
• Active-First Washout: mean -9.50 versus -10.20 on control; difference 0.70 (95% CI -5.40 to 6.80), standardized effect d = 0.05; z-test p = 0.822.
• Active-First-Then-Sham Washout: mean -11.00 versus -10.20 on control; difference -0.80 (95% CI -7.46 to 5.86), standardized effect d = -0.05; z-test p = 0.814.
• Sham First: mean -3.70 versus -10.20 on control; difference 6.50 (95% CI 1.32 to 11.68), standardized effect d = 0.56; z-test p = 0.014.

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 Tinnitus Bandwidth/Spectrum (TinnTester Interactive Software)

• 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:
  • Active First: mean 7.10 versus 9.50 on control; difference -2.40 (95% CI -5.04 to 0.24), standardized effect d = -0.40; z-test p = 0.074.
  • Active-First Washout: mean 8.40 versus 9.50 on control; difference -1.10 (95% CI -3.87 to 1.67), standardized effect d = -0.18; z-test p = 0.437.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active First and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active-First Washout and the control. The interval gives the range of effects that remain compatible with the data.

Changes in Minimum Masking Level (MML)

• 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:
  • Active First: mean -5.10 versus -2.00 on control; difference -3.10 (95% CI -4.25 to -1.95), standardized effect d = -1.19; z-test p = <0.001.
  • Active-First Washout: mean -1.10 versus -2.00 on control; difference 0.90 (95% CI -0.26 to 2.06), standardized effect d = 0.34; z-test p = 0.127.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Active First than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active-First Washout and the control. The interval gives the range of effects that remain compatible with the data.

Tinnitus Hearing Survey

• 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:
  • Active First: mean -0.70 versus -0.90 on control; difference 0.20 (95% CI 0.00 to 0.40), standardized effect d = 0.44; z-test p = 0.049.
  • Active-First Washout: mean -1.80 versus -0.90 on control; difference -0.90 (95% CI -1.10 to -0.70), standardized effect d = -1.99; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Active First than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Active-First Washout than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover tinnitus bandwidth or spectrum, minimum masking level, and the Tinnitus Hearing Survey. They measure different aspects of tinnitus and use different units and dispersion summaries. Across these outcomes, the posted means vary by sequence and period, and the comparisons do not form a uniformly consistent pattern. Some unadjusted comparisons have intervals that include zero, while others do not. This mixed pattern does not amount to a single overall finding across the secondary outcomes.

The secondary results complement the primary outcome by describing other measurements collected during the same crossover schedule. They do not directly validate the primary endpoint because they assess different constructs, and the registry does not report a prespecified strategy for combining them. The secondary outcomes are also subject to the same interpretive concerns as the primary endpoint: multiple periods, repeated participant representation, possible spillover, and a lack of reported detail on the analysis model and missing data.

The registry lists three secondary outcomes but posts no sponsor-reported analyses for them. The comparisons available in the record are unadjusted. General statistical explanation: when many outcomes and contrasts are examined, the chance of at least one apparently notable result can increase. Without a reported multiplicity procedure or a hierarchy of prespecified tests, individual secondary p-values carry less weight than a result from a clearly defined primary analysis. They are best viewed as descriptive or exploratory evidence rather than independent confirmation of a treatment effect.

The secondary summaries should therefore be interpreted as a set of related measurements, not as separate definitive tests. Their variation may reflect true differences, random uncertainty, different measurement properties, or the timing and sequence of assessment. The record does not report a clinical-importance threshold for these measures, so statistical comparisons alone do not establish whether a numerical change matters to participants.

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

• Change in Tinnitus Bandwidth/Spectrum (TinnTester Interactive Software)
• Changes in Minimum Masking Level (MML)
• Tinnitus Hearing Survey

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports continuous outcomes as means. A mean is a way to summarize the center of numerical measurements; it does not show how each participant changed. For the primary outcome, the posted summaries include a standard error alongside each mean. A standard error describes the uncertainty of an estimated mean, rather than the spread of individual participants’ measurements. Standard deviations, where posted for secondary outcomes, describe variation among measurements and are not interchangeable with standard errors.

What does the crossover structure imply?

In a crossover study, the same participant can experience different treatment conditions at different times. This can allow comparisons within a participant, but it also makes sequence, period, and possible carryover important. A washout interval is intended to separate treatment periods, but its presence does not by itself demonstrate that prior treatment effects have ended. The registry’s primary outcome description explicitly says participants are represented more than once across trial segments to assess possible spillover. Segment counts therefore do not represent mutually exclusive groups of participants.

The record lists randomized treatment order and quadruple masking. Those design labels describe allocation and masking at a broad level; they do not tell the reader which statistical model was used, how repeated measurements were handled, or how period and carryover effects were assessed. The original statistical model and analysis plan are not reported in the registry record. It is therefore not possible to confirm from the record whether the posted period comparisons fully account for the crossover structure.

How should the mean differences be read?

The posted comparison estimates are mean differences between a named segment and the reference segment, Active-First Then Sham. For example, the Active First comparison is 4.1, with the interval and unadjusted p-value reported alongside it. The sign depends on the order used in the comparison calculation; it should not be translated into benefit or harm without a justified treatment contrast and a clear clinical interpretation of the scale. Because the reference is one segment rather than a simple pooled sham condition, these estimates should not be relabeled as the overall active-versus-sham effect.

The comparison summaries include confidence intervals and unadjusted p-values. A confidence interval gives a range of values compatible with the estimate under the calculation and assumptions used. The interval also shows precision: a wider interval indicates greater uncertainty about the comparison. If an interval includes zero, a zero mean difference is among the values compatible with the interval at its stated confidence level. This does not prove that the groups or periods are equal. If it excludes zero, that indicates that zero is outside the interval under the same calculation; it does not establish clinical importance or eliminate biases from the study design.

What does an unadjusted p-value describe?

General statistical explanation: a p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of a difference. The p-values in the posted comparisons are labelled unadjusted. The registry does not report a multiplicity adjustment or a sponsor analysis for these comparisons. Considering several outcomes and periods without adjustment increases the chance of finding one or more small p-values even when there is no underlying difference for some or all comparisons.

The displayed comparisons are simple, unadjusted comparisons calculated from posted summary statistics. They are not presented as sponsor-reported analyses; the record lists no analyses for the primary endpoint. The registry does not report the sponsor’s model, analysis population, handling of missing observations, or rules for choosing the reported contrasts. Those details should not be inferred from the numerical summaries alone.

Why does variability matter?

General statistical explanation: greater variability makes it harder to distinguish a real difference from random variation, all else being equal. For a continuous outcome, the estimated uncertainty depends on the number of observations and how variable the measurements are. In a crossover design, however, the relationship between repeated measurements within the same participant is also relevant. Separate group summaries do not reveal that within-person relationship. A calculation based only on posted means and standard errors cannot recover every feature of a paired or repeated-measures analysis.

Some secondary outcomes report standard deviations, while others report standard errors. These describe different aspects of the data. The registry’s summaries should be interpreted according to the measure attached to each outcome, rather than comparing spreads across outcomes as if they were on a common scale. The measurement units differ, too: dB SL, dB sensation level, units on a scale, and score on a scale are not directly interchangeable.

What can the posted results establish?

The summaries establish what means and comparisons were posted for the listed segments. They do not by themselves establish the effect of active stimulation relative to sham, the persistence of any change, or the clinical value of a change. A complete interpretation would require a clear estimand, the prespecified analysis method, information about participants with missing data, and appropriate handling of sequence, period, and within-participant correlation. These details are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is conveyed primarily by the confidence intervals around the reported mean differences. For the primary outcome, the interval for Active First extends from -1.624 to 9.824, while the interval for Sham First extends from 1.322 to 11.68. The former includes zero and the latter does not. Other comparisons have intervals of varying width; several include zero, and the Sham-First Washout interval runs from 0.118 to 10.88. These ranges show that the estimates are not equally precise and should not be reduced to a yes-or-no reading of their p-values.

General statistical explanation: a confidence interval is a range produced by a method that, under its assumptions, has a stated long-run coverage property. It is not a guarantee that the true value lies within one particular calculated interval. The interval’s width reflects statistical uncertainty under the calculation. It does not include every possible source of uncertainty, such as measurement error, bias, inappropriate modeling, missing outcomes, or an unsuitable choice of contrast.

The primary summaries report standard errors, but the record does not post confidence limits for each segment mean. The comparison intervals are unadjusted and are based on comparisons between listed periods. They do not show uncertainty from a sponsor-reported crossover model, and the registry does not report whether correlation among repeated observations was incorporated. In a crossover study, that information can matter substantially to the precision of a treatment contrast.

The intervals should be read alongside the design and the measured scale. An interval that includes zero does not prove equivalence; an interval that excludes zero does not establish clinical importance. A threshold for meaningful change is not reported in the registry record. Accordingly, the posted intervals describe statistical precision for the listed calculations, not certainty about the broader clinical interpretation.

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 derived from observed comparison effects, not enrollment targets from the original study design. For these continuous outcomes, the figures are participants per arm, not total events. The planning assumptions listed in the registry are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding number for a higher chance of detection under the same assumptions. These are design calculations, not statements about the probability that the observed study result is correct. They are not observed power.

The rows that plan for 100%, 75%, or 50% of the observed effect illustrate how the assumed effect size changes the planning estimate. A smaller effect is harder to distinguish from random variation, so detecting a smaller effect generally requires more participants. The figures can become especially large when the observed comparison is small relative to its variability; they should not be read as recommendations for a future trial without a justified target effect and suitable design assumptions.

The calculations use a two-arm approximation. The trial itself is a crossover study with repeated measurements and possible spillover, so the planning illustration may not represent the requirements of a future crossover analysis. The original protocol assumptions, any adjustment for the crossover structure, and any interim-analysis plan are not reported in the registry record.

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 = 4.100; pooled standard deviation σ = 12.986.
2. n = 2 × (1.96 + 0.842)² × 12.986² / 4.100² = 157.5, rounded up to 158 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 <- 4.1                      # observed difference in means
sigma <- 12.9858799056158                     # 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(3621735)
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 = 158 (80% power), 211 (90% power)
 75% of observed effect: n per arm = 280 (80% power), 375 (90% power)
 50% of observed effect: n per arm = 630 (80% power), 844 (90% power)
power.t.test: 158.4 
Simulated power at n = 158 per arm: 0.796 (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 lists one primary outcome and three secondary outcomes, with multiple trial segments and comparisons reported for the outcomes. The posted comparison p-values are unadjusted. A multiplicity plan, including whether any outcomes or contrasts were prioritized beyond their labels, is not reported in the registry record. Without that information, individual small p-values should be interpreted cautiously: the more comparisons considered, the more opportunities there are for an apparently unusual result to occur by chance.

The record does not report a sponsor analysis for the primary outcome, and the secondary outcomes have no reported analyses. It also does not report the prespecified analysis population, exclusions from the analysis, or whether all randomized participants were included in each outcome analysis. The counts differ across trial segments, but the registry’s note about repeated participant representation means those counts are not a count of distinct participants across the whole study. Reasons for changes in segment counts are not reported in the registry record.

Missing-data methods are not reported in the registry record. The record does not say how incomplete weekly assessments, withdrawal, or missing period measurements were handled. Nor does it describe any sensitivity analysis for missing data. In a crossover study, missing measurements in one period can affect whether a participant contributes to a paired comparison or to a particular sequence analysis. The posted summary statistics do not show enough detail to assess that issue.

The registry also does not report how the analysis addressed the order of treatment, period effects, within-participant correlation, or possible carryover. The outcome description says spillover was a concern, but a method for assessing or adjusting for it is not reported. These omissions do not make the posted values unusable as descriptive summaries; they limit the strength of inferential conclusions that can be drawn from them.

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.

Most frequent non-serious adverse event terms

The registry reports serious adverse event counts separately for the pre-use period, active treatment, active washout, sham treatment, sham washout, and post-study monitoring. The reported serious adverse event count is 0 in each of these groups. The record also reports 0 deaths in each group. The numbers at risk differ by period, and participants may appear in more than one period because this is a crossover study. These group counts should not be added together as if each represented a separate set of people.

These figures describe the serious adverse events recorded in the registry’s listed periods. They do not establish that no serious event could occur, nor do they by themselves permit a comparative safety estimate between active and sham treatment. The registry does not list serious adverse event terms. The reported serious-event counts are distinct from the counts of other, non-serious adverse events, which are also posted for the periods.

The record does not provide detailed event narratives or an analysis comparing event rates across treatment conditions. Follow-up duration and completeness for safety ascertainment beyond the listed periods are not reported in the registry record. The counts should therefore be read as the posted safety summary, not as a comprehensive conclusion about safety.

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

The posted results describe changes in TinnTester estimates and other tinnitus measures across a randomized crossover trial of active and sham stimulation. They show that mean outcome values differed across some segments and that the size and precision of calculated contrasts varied. The primary outcome comparisons include both intervals that cross zero and intervals that do not. This is a description of the posted data and calculations, not a conclusion that the intervention is effective or ineffective.

A segment comparison is not automatically equivalent to the causal contrast a reader may want. The trial includes two treatment sequences, multiple periods, and washout periods, and the registry notes possible spillover. The reference for the posted comparisons is one particular segment, rather than an explicitly reported overall active-versus-sham contrast. The original analysis method and its handling of crossover features are not reported in the registry record. This limits how confidently the calculations can be interpreted as treatment effects.

Statistical evidence and clinical importance are different questions. A confidence interval that excludes zero indicates that zero is outside the interval under the calculation used; it does not tell whether the difference is large enough to matter to participants. An interval that includes zero does not prove that no meaningful effect exists. The registry does not report a threshold for clinically important change in tinnitus loudness or in the secondary measures.

The outcomes are based on a computerized estimate and other reported measures. They should be understood as measurements, not as a complete account of participants’ experience or quality of life. Although the study’s summary states a goal of improving quality of life, the posted primary endpoint is objective tinnitus loudness and the listed secondary measures concern spectrum, masking level, and a hearing survey. The registry does not report a separate quality-of-life result among the listed outcomes.

Accordingly, the posted data support a careful description of observed means, comparisons, and uncertainty. They do not alone establish the durability of change, the clinical importance of the numerical differences, or an overall causal effect. Those questions depend on analysis details and context that are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial raises statistical questions that are common in crossover studies of interventions delivered over time. Participants receive both active and sham conditions, so the sequence and period of exposure are part of the comparison. A washout period can be relevant to possible carryover, but its inclusion does not demonstrate that carryover is absent. The registry itself identifies spillover as a concern, making the treatment sequence and the structure of repeated measurements important to interpretation.

The posted outcome summaries make clear that a trial’s data can be organized into multiple treatment and washout segments. Those segments are useful for describing the schedule, but they should not be mistaken for independent groups or for a direct overall contrast. The repeated representation of participants also emphasizes why group means and standard errors may not convey the full dependence structure of crossover data. Appropriate interpretation depends on knowing how that structure was handled.

The record also illustrates the distinction between descriptive outcome reporting and a reported inferential analysis. It contains means, standard errors, comparison estimates, intervals, and unadjusted p-values, but no sponsor-reported analyses are listed. Without a reported model and analysis plan, readers can examine the posted summaries while recognizing that they may not capture the trial’s complete statistical analysis.

Finally, the planning illustrations show how assumptions about the effect to detect affect sample-size planning. They are not a substitute for the original trial’s justification, which is not reported in the registry record. Separating planning calculations from observed evidence—and statistical differences from clinically meaningful changes—is essential when reading results from this type of design.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations specific to this trial affect interpretation. First, the primary outcome is organized across multiple periods in two randomized sequences, and the registry notes that participants are represented more than once to assess spillover. The posted segment summaries do not show the within-participant relationships among repeated measurements. The record does not report a model that accounts for those relationships, sequence, period, or carryover.

Second, the primary comparison estimates use Active-First Then Sham as their reference. That makes the posted contrasts comparisons with a particular period, not a clearly reported overall active-versus-sham treatment contrast. The protocol’s intended primary estimand and sponsor’s prespecified analysis are not reported in the registry record. Consequently, it is not possible to establish from these summaries whether the posted contrasts match the original primary analysis.

Third, counts vary across the segments, and the registry does not explain the reasons for those differences. It does not report missing-data methods, participant flow by sequence, or a complete analysis population definition. These gaps limit assessment of whether incomplete measurements could affect comparisons.

Fourth, several outcomes and period comparisons are presented with unadjusted p-values. A multiplicity strategy is not reported, and secondary analyses are not listed. Individual p-values therefore require caution. The record also does not report clinically important thresholds for the measures, leaving the practical meaning of numerical changes uncertain.

Finally, the brief summary describes intended enrollment up to 300, while registry enrollment is 100; the reason for this difference is not reported. The intervention labels use both Burst-SCS terminology and descriptions of bimodal auditory-somatosensory stimulation, without a reported explanation of the naming difference. These record-level ambiguities should be kept distinct from the numerical results themselves.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Reversing Synchronized Brain Circuits With Targeted Auditory-Somatosensory Stimulation to Treat Phantom Percepts — NCT03621735.
• Registry record last updated 2023-08-30; status last verified 2023-08.
• Results first posted 2023-08-30.
• 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

NCT03621735 is a completed, randomized, quadruple-masked crossover study sponsored by the University of Michigan. It enrolled 100 participants and examined active and sham bimodal auditory-somatosensory stimulation for tinnitus, with treatment order randomized and washout periods included.

The primary endpoint was change in objective tinnitus loudness measured by TinnTester in dB SL. The registry posts means and standard errors by sequence and period, along with unadjusted comparisons against the Active-First Then Sham segment. The primary comparison results vary in precision; some intervals include zero and some do not. Three secondary outcomes are also posted, with no sponsor-reported analyses listed.

The record reports no serious adverse events or deaths in the listed periods. The original analysis plan, missing-data methods, multiplicity strategy, crossover model, and clinical-importance thresholds are not reported in the registry record. The posted summaries describe the recorded values but do not alone establish a definitive overall treatment effect or clinical importance.