Phase 3 Clinical Trial: D-methionine to Reduce Noise-Induced Hearing Loss (NIHL): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 3 Clinical Trial: D-methionine to Reduce Noise-Induced Hearing Loss (NIHL) (NCT02903355), a randomized phase 3 study. The primary outcome is ASHA Shift Ear (Left).

2. Clinical Question

The study's stated objective was to assess prevention of noise-induced hearing loss or reduction of tinnitus associated with weapons training. The posted primary endpoint is narrower: it counts participants meeting a specified left-ear hearing-shift definition. Tinnitus was addressed among the secondary outcomes, rather than being part of this primary endpoint. The record does not report a primary endpoint result for the right ear.

3. Trial Design

The registry record identifies a Phase 3 randomized trial with quadruple masking and a parallel-group model. Participants were assigned to oral D-methionine or placebo. The sponsor was Southern Illinois University, and the recorded enrollment was 351. The trial status is terminated. The record lists a start date of 2013-09 and a primary completion date of 2017-12.

The study population was a cohort of Drill Sergeant instructor trainees during and after weapons training. The training context is described as an 11 day period with a minimum of 500 rounds of M-16 weapons training. The primary endpoint timeframe was change from baseline to day 29-36 after initial study-drug administration, described also as day 15-22 after cessation of weapons training.

The registry identifies placebo and D-methionine as the interventions and describes the placebo as matched in flavor and color. Although the brief summary characterizes the study as double-blind, the design field records quadruple masking; the registry record does not specify the roles included in that masking designation. Dosing details, treatment adherence, the exact randomization procedure, allocation concealment, and the reasons for termination are not reported in the registry record.

The recorded enrollment is not the same as the analyzed sample for every outcome. For the primary left-ear outcome, 5 participants in the placebo arm and 3 in the D-methionine arm failed a final tympanogram screen and were excluded from that outcome analysis. The record does not provide a complete account of all exclusions, withdrawals, or missing outcome measurements. It also does not report the trial's original sample-size justification or the reasons the trial ended with terminated status.

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

Analysis population for the primary outcome, as defined in the registry: 5 and 3 participants in the placebo and D-methionine arms, respectively, failed a final tympanogram screen in the left ear to rule out middle ear pathology as a cause of the hearing loss and were excluded from the analysis for this outcome.

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 ASHA Shift Ear (Left), measured over Change from baseline to day 29-36 after initial administration of study drug (Day 15-22 after cessation of weapons training)..

The primary endpoint is the count of participants with an ASHA shift in the left ear. The registry defines a shift as an increase of at least 20 dB at any one frequency, an increase of at least 10 dB at any two consecutive frequencies, or loss of response at 3 consecutive frequencies where responses had been obtained at baseline. This rule turns hearing-test changes into a binary outcome: each participant either meets the shift definition or does not.

The endpoint compares the assessment with baseline, at day 29-36 after initial study-drug administration, or day 15-22 after weapons training ceased. A standardized threshold-based definition can make a change in hearing easier to classify consistently than an unstructured description of test results. It also allows the outcome to be expressed as the proportion of participants meeting the criterion in each arm.

The registry states that 5 placebo participants and 3 D-methionine participants failed the final left-ear tympanogram screen and were excluded from this analysis, because middle-ear pathology could be a cause of hearing loss. The endpoint therefore reflects the analyzed participants who remained eligible after that screen, not every enrolled participant. The record does not report additional details about endpoint adjudication or how missing hearing assessments were handled.

7. Results Posted in the Registry

• D-methionine, Oral Liquid Suspension: 7.4% (9/121) versus 8.8% (12/137) on control; risk difference -1.3 percentage points (95% CI -8.0 to 5.3), risk ratio 0.85 (0.37–1.95); unadjusted two-proportion z-test p = 0.699.

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.

DOEHRSHC Shift

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • D-methionine, Oral Liquid Suspension: 1.6% (2/123) versus 1.4% (2/142) on control; risk difference 0.2 percentage points (95% CI -2.7 to 3.2), risk ratio 1.15 (0.17–8.07); unadjusted two-proportion z-test p = 0.885.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between D-methionine, Oral Liquid Suspension and the control. The interval gives the range of effects that remain compatible with the data.

EWS STS Shift

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • D-methionine, Oral Liquid Suspension: 4.1% (5/123) versus 7.7% (11/142) on control; risk difference -3.7 percentage points (95% CI -9.3 to 1.9), risk ratio 0.52 (0.19–1.47); unadjusted two-proportion z-test p = 0.210.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between D-methionine, Oral Liquid Suspension and the control. The interval gives the range of effects that remain compatible with the data.

Total THI Score Change

• 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:
  • D-methionine, Oral Liquid Suspension: mean -0.15 versus 0.17 on control; difference -0.31 (95% CI -1.36 to 0.73), standardized effect d = -0.07; z-test p = 0.556.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between D-methionine, Oral Liquid Suspension and the control. The interval gives the range of effects that remain compatible with the data.

Across the posted secondary outcomes, the point estimates do not form a consistent pattern of clear separation between the arms. The recalculated confidence intervals for the secondary comparisons include zero, and the sponsor-reported p-values do not provide a pattern of strong evidence across outcomes. This overall picture is broadly consistent with the imprecision of the primary result rather than presenting a clear, independent contrast.

Secondary outcomes address different aspects of hearing or tinnitus and are not interchangeable with the primary left-ear ASHA shift endpoint. Some are participant counts meeting shift or change criteria, while Total THI Score Change is a continuous score outcome. Differences in outcome definition, scale, and analysis mean that their estimates should not be combined into a single conclusion. They can provide context, but they do not replace the primary comparison.

Unadjusted secondary results carry less weight when multiple outcomes are examined because the chance of at least one apparently unusual finding increases as the number of tests grows. The registry lists several secondary outcomes but does not report a multiplicity adjustment, an outcome hierarchy, or whether the analyses were designated confirmatory or exploratory. A result from one secondary endpoint should therefore not be treated as a stand-alone confirmation of the primary result. The secondary findings are best read as additional, uncertain descriptions of the posted data.

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

• DOEHRSHC Shift
• EWS STS Shift
• Total THI Score Change
• Significant Change in Tinnitus

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: a participant either meets the ASHA shift criterion or does not. The arm-level results are counts and denominators, and the comparison is expressed as a risk difference. A risk difference subtracts the event proportion in the comparator arm from the event proportion in the intervention arm; the posted value is -0.013. Negative values indicate a lower observed event proportion in the D-methionine arm under this comparison's direction. This description concerns the arithmetic meaning of the estimate, not a conclusion about treatment benefit.

What does the confidence interval represent?

A confidence interval describes the uncertainty around an estimate under the statistical method used to construct it. For the primary risk difference, the posted interval runs from -0.080 to 0.053. Because it includes zero, the results are compatible with no between-arm difference as well as with differences in either direction. The interval is not a guarantee that the true value lies within its limits, and it does not identify which value is most plausible without additional assumptions.

How should the p-values be read?

The registry reports a Fisher Exact test for the primary comparison, with p = .4385. Fisher's Exact test is a method for comparing categorical outcomes using the observed counts in the groups. The separate unadjusted recalculation reports p = 0.699. A p-value measures how unusual results at least as incompatible with a specified null hypothesis would be under that hypothesis and the test's assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect.

The two p-values differ, while the record does not give sufficient information to account for the difference. The registry does not report a confidence interval or effect estimate alongside its Fisher Exact result. The recalculated risk difference and interval are based on the posted summary counts and are not a substitute for a more fully specified sponsor analysis.

What does masking contribute?

The design field records quadruple masking, which indicates that masking was part of the trial design, but the registry record does not identify the roles covered by that label. In general, masking can reduce the influence of expectations on participant reports, clinical decisions, and outcome assessment. The record does not describe how masking was maintained or assessed, so those details cannot be evaluated from the posted information.

The parallel-group design compares participants assigned to different arms over the trial rather than describing a crossover. Randomized allocation is recorded, but the method used to generate the allocation sequence and the approach to conceal assignment are not reported in the registry record. Those details matter for judging how well randomization could balance factors between groups and prevent foreknowledge of assignment.

What is the role of the secondary analyses?

The registry posts binary secondary outcomes and one continuous secondary outcome. For binary outcomes, the comparison is also presented as a risk difference. For the Total THI Score Change outcome, the comparison is a difference in means. The reported sponsor methods include Fisher Exact tests for the binary secondary outcomes and a one-sided t-test for the continuous outcome. A t-test compares group means relative to the observed variability and sample size; the registry does not provide a sponsor-reported confidence interval for that test.

The recalculated secondary comparisons are unadjusted. A confidence interval for a mean difference describes uncertainty in the estimated difference between group averages. Standard deviations describe spread among individual observations, which is different from uncertainty in the estimated average. For Total THI Score Change, the record gives the arm means, standard deviations, and a recalculated mean difference and interval. These are descriptive and inferential summaries of the posted data, not proof of a causal effect.

General statistical context: when a study examines several outcomes, chance alone can make at least one result appear noteworthy even if there is no underlying effect. Adjustment for multiplicity can address that issue, but the registry record does not report a multiplicity procedure. It also does not report a prespecified hierarchy or explain whether any secondary analyses were exploratory. The secondary results should consequently be read as supportive descriptions rather than as independent confirmation of the primary finding.

The record does not report the full statistical analysis plan, the analysis population definitions, or the treatment of all missing observations. It also does not report whether interim analyses were planned or conducted. These are not details that can be inferred from the posted arm counts or p-values.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.013, and its confidence interval extends from -0.080 to 0.053. The interval includes zero and permits differences in either direction. Its span indicates that the point estimate alone should not be read as a precise description of the underlying between-arm difference. The available sample counts and event counts leave considerable uncertainty around the estimate.

The registry-reported Fisher Exact result is p = .4385, while the unadjusted recalculation gives p = 0.699. The registry record does not report a sponsor confidence interval for the primary comparison, so the recalculated interval is the posted interval available for describing precision. Because the record does not explain the different p-values, they should not be treated as interchangeable outputs from a single fully documented analysis.

Precision is distinct from whether a result crosses a threshold used for statistical significance. A wide interval can include the null value and still include effects that may matter in either direction. The interval does not prove that the true effect is zero, and the point estimate does not prove that the observed difference will recur. For the primary endpoint, the appropriate reading is that the observed data leave uncertainty about the direction and size of any difference.

The exclusions after the final tympanogram screen are also relevant to precision and interpretation: 5 placebo participants and 3 D-methionine participants were excluded from this outcome analysis. The record does not give complete information about other missing data or the sensitivity of the result to analysis choices. Those omissions limit assessment of how robust the interval is to alternative handling of unavailable or excluded observations.

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 illustrations express sample sizes as participants per arm, not as total participants across the trial and not as total events. They are based on the observed effect and the listed planning assumptions: two-sided significance level 0.05, equal allocation between the two arms, a normal approximation, and detection of the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column represents the planned number of participants per arm under those assumptions for an analysis to have an 80% chance of detecting the specified effect, if that effect and the model assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally requires a larger planned sample under the same assumptions. These are planning calculations, not statements about what the trial achieved.

The rows that use 100%, 75%, and 50% of the observed effect illustrate how the planning sample changes when the effect to detect is smaller. Smaller effects need more participants to distinguish them from random variation at the same significance and power settings. The figures are illustrations based on the observed effect, not evidence that the trial was designed around that effect. This is not observed power.

The displayed planning values should not be interpreted as a retrospective judgment that the trial was adequately or inadequately designed. The registry record does not report the original assumptions used to plan enrollment, and the planning illustrations use simplified assumptions that may not match the study's actual design or analysis.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.088; treatment proportion p₁ = 0.074; average p̄ = 0.081.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3858 = 0.7562.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3857 = 0.3246.
4. n = (0.7562 + 0.3246)² / (-0.0132)² = 6,692.9, rounded up to 6,693 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0875912408759124                          # control proportion
p1 <- 0.0743801652892562                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2903355)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 6,693 (80% power), 8,960 (90% power)
 75% of observed effect: n per arm = 12,121 (80% power), 16,226 (90% power)
 50% of observed effect: n per arm = 27,768 (80% power), 37,172 (90% power)
power.prop.test: 6692.9 
Simulated power at n = 6,693 per arm: 0.798 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

For the primary outcome, the registry reports a Fisher Exact test with p = .4385. The unadjusted recalculation based on the posted counts gives p = 0.699 and a risk difference of -0.013 with a confidence interval from -0.080 to 0.053. These are different p-values. The record does not report enough detail to explain the difference, and it does not give a sponsor-reported confidence interval or effect estimate for the primary comparison.

The registry record does not flag a discrepancy between the posted outcome counts and its reported analysis. The recalculation is a simple, unadjusted analysis of those counts, whereas the sponsor's reported method is Fisher Exact. The recalculation should therefore be read as a check and an additional description of the posted data, not as a replacement for the sponsor's analysis. The registry does not give further information about choices that could clarify how the two p-values were obtained.

The sponsor's reported p-value alone does not show the magnitude or precision of the difference. The recalculated risk difference and interval add that information, while remaining limited to the posted summary counts and the specified unadjusted method. Both analyses should be understood in the context of the endpoint definition, its exclusions, and the incomplete reporting of the analysis plan.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists four secondary outcomes in addition to the primary endpoint, and it posts analyses for the secondary outcomes. Testing several outcomes can increase the chance of observing a nominally unusual result by chance. Statistical approaches such as adjustment of significance thresholds, hierarchical testing, or a prespecified outcome sequence can address multiplicity in different ways. The registry record does not report whether any such approach was planned or used.

The record also does not report a complete statistical analysis plan, including whether the primary endpoint and analysis were finalized before examining outcome data. Interim analyses and any rules for stopping early are not reported in the registry record. The trial status is terminated, but the reason for termination and whether it involved prespecified statistical criteria are not reported in the registry record.

For the primary endpoint, the registry notes a specific exclusion: 5 placebo participants and 3 D-methionine participants failed the final left-ear tympanogram screen and were excluded from that outcome analysis. The record does not fully describe the analysis population, the disposition of all randomized participants, or how other missing measurements were handled. It does not report an intention-to-treat analysis or a sensitivity analysis for missing or excluded observations. Consequently, the effect of those analysis decisions on the result cannot be assessed from the posted record.

These reporting gaps do not establish that a particular method was or was not used. They mean that readers cannot verify those details from the registry record. The endpoint-specific exclusion should be considered when interpreting the analyzed counts, while avoiding assumptions about unreported exclusions, missingness, interim monitoring, or multiplicity procedures.

16. 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 safety record lists 159 participants at risk in the placebo group and 157 in the D-methionine group for serious adverse events. It records 0 serious adverse events affecting participants in either group and 0 deaths in either group. The registry's serious adverse-event terms list is empty. These entries describe what was posted; they do not establish that no events of any kind occurred outside the registry's reporting categories.

For other adverse events, the record lists 93 affected participants among 159 at risk in the placebo group and 120 affected participants among 157 at risk in the D-methionine group. These are counts of participants with other adverse events, not counts of all events. The registry does not provide a breakdown by event type or severity in the listed figures.

Safety counts require context about ascertainment, exposure, follow-up, and event definitions. Those details are not reported in the registry record. The counts should not be used alone to infer comparative safety, particularly because the record does not supply a statistical comparison or a full description of the safety analysis.

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

The posted primary data show that 12 of 137 placebo participants and 9 of 121 D-methionine participants met the defined left-ear ASHA shift criterion. The recalculated risk difference is -0.013, with an interval from -0.080 to 0.053. This is an uncertain estimate: the interval includes zero and allows for differences in either direction. The registry-reported Fisher Exact p-value is .4385, while the unadjusted recalculation gives 0.699; the record does not explain the difference.

These results do not establish that D-methionine prevents noise-induced hearing loss or reduces tinnitus. The primary endpoint concerns a particular threshold-based left-ear classification at a specified follow-up, not every possible hearing outcome. Nor do the results establish that the intervention and placebo are equivalent. A lack of a clearly separated result is not proof of no effect, especially when the estimate is imprecise.

The study's stated aim included hearing loss and tinnitus, but the posted primary endpoint is the left-ear shift measure. Tinnitus-related measures appear among the secondary outcomes and should be interpreted with the limitations of multiple unadjusted comparisons and incomplete analysis-plan reporting. Findings from those outcomes do not change what the primary endpoint measures.

The registry reports outcome-specific exclusions after tympanogram screening and does not provide a full account of missing data, analysis populations, or the reason for termination. These limits restrict how completely the results can be assessed. The appropriate conclusion is descriptive: the posted data show the observed counts and an uncertain estimated difference, while important questions about the original design and analysis remain unreported.

18. Why This Trial Matters Statistically

This trial illustrates why an observed difference, a p-value, and a confidence interval answer different statistical questions. The count comparison describes what occurred among analyzed participants; the risk difference expresses the contrast in event proportions; and the interval conveys uncertainty about that contrast. Considering these together avoids relying on a single threshold or statistic.

It also highlights the importance of endpoint definition. The primary result is not a general measure of hearing or tinnitus, but a specific left-ear classification based on threshold changes and loss of response. The final tympanogram exclusions further define who contributed to that outcome. Clear endpoint and analysis-population reporting is necessary for understanding what a result represents.

The difference between the registry's Fisher Exact p-value and the unadjusted recalculation is another statistical reporting issue. A transparent account of the analysis method, effect estimate, interval, missing-data rules, and analysis population makes it easier to interpret how results relate. Here, several of those details are not reported in the registry record, so the posted summary supports a limited assessment rather than a complete reconstruction of the analysis.

Finally, the trial provides an example of the distinction between a planning calculation and observed evidence. Sample-size illustrations based on the observed effect do not reveal the assumptions behind the trial's original enrollment plan and do not measure the probability that the trial detected an effect. Keeping planning and inference separate is essential when reading clinical trial results.

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.

Several limitations specific to this record constrain interpretation. The primary outcome analysis excluded 5 placebo participants and 3 D-methionine participants who failed the final left-ear tympanogram screen. Although the registry explains that the screen was intended to rule out middle-ear pathology as a cause of hearing loss, it does not report a full disposition of participants or how other missing outcome data were handled.

The recorded enrollment is 351, but the primary analysis denominators are 137 and 121. The registry does not explain all differences between enrollment and those outcome-specific denominators. It also does not report the original sample-size calculation, the intended analysis populations, the allocation-generation procedure, or the detailed analysis plan. Reasons for the terminated status are not reported in the registry record.

The registry reports a Fisher Exact p-value for the primary comparison, while the unadjusted recalculation from the posted counts produces a different p-value. The record does not provide enough methodological detail to reconcile them, and it does not post a sponsor-reported confidence interval for the primary comparison. The recalculated interval is useful for describing the summary counts, but it does not resolve that reporting gap.

Multiplicity procedures for the several secondary outcomes, interim analyses, and sensitivity analyses are not reported in the registry record. Masking is recorded as quadruple, but the roles masked and the methods used to maintain masking are not described. These limits do not prove that procedures were absent; they restrict what can be verified from the registry information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase 3 Clinical Trial: D-methionine to Reduce Noise-Induced Hearing Loss (NIHL) — NCT02903355.
• Registry record last updated 2022-06-28; status last verified 2022-06.
• Results first posted 2022-06-28.
• 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

The registry describes a randomized, quadruple-masked, parallel Phase 3 trial comparing oral D-methionine with placebo among Drill Sergeant instructor trainees undergoing weapons training. Recorded enrollment was 351, and the status is terminated. The primary endpoint was the count of participants with an ASHA-defined left-ear shift at the stated post-training assessment.

The primary analysis included 137 placebo participants and 121 D-methionine participants, after the reported tympanogram exclusions. The posted counts were 12 and 9, respectively. The registry reports a Fisher Exact p-value of .4385; an unadjusted recalculation gives a risk difference of -0.013 with a confidence interval from -0.080 to 0.053 and p = 0.699. The record does not explain the difference between the p-values.

Secondary outcomes and safety counts are also posted, but multiplicity procedures, complete missing-data handling, original sample-size assumptions, and reasons for termination are not reported in the registry record. The primary estimate is uncertain and should be interpreted as a description of the posted analysis rather than as a definitive conclusion about treatment effect.