Randomized Trial Comparison of Ototoxicity Monitoring Programs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized Trial Comparison of Ototoxicity Monitoring Programs (NCT02099786), a randomized na study. The primary outcome is Number of Participants With an Ototoxic Hearing Shift.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, parallel-group trial comparing COMP-VA with usual care. It reports single masking, but does not identify which participants, clinicians, assessors, or other parties were masked. The study is listed as completed, with enrollment of 47. Its dates are 2015-04-01 for study start and 2018-05-05 for primary completion. The phase is listed as NA.

COMP-VA was a portable hearing-monitoring program. Its arm description specifies hearing testing at each cisplatin treatment and at 1 month following treatment. The study summary describes portable audiometry and efficient tools and techniques intended to make testing possible before each treatment at a quiet location in the hospital. Usual care followed the Audiology Clinic protocol. The registry record does not report further details about how randomization was generated, whether allocation was concealed, or how adherence to either monitoring approach was assessed.

The posted primary outcome is the number of participants with an ototoxic hearing shift, with a stated timeframe of 35 days post randomization. The outcome description refers to ASHA-significant threshold shifts and CTCAE grade 1 or greater hearing shifts. The primary outcome counts are 15 participants among 21 listed for COMP-VA and 8 among 15 listed for usual care. These arm-specific outcome denominators are not the same as the registry's overall enrollment figure, and the record does not explain the difference or describe the analysis population in detail.

The registry record lists four outcome measures and five analyses. It does not report the original sample-size justification, its anticipated effect, or the planned statistical analysis in enough detail to establish how the trial was designed to answer the primary question. A planning illustration based on the observed effect is distinct from that original design information.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With an Ototoxic Hearing Shift, measured over 35 days post randomization.

The primary endpoint is the number of participants with an ototoxic hearing shift, assessed at 35 days post randomization. It is a binary participant-level outcome: each participant is counted according to whether a qualifying hearing shift was recorded. The registry description gives two types of qualifying shift. An ASHA shift is defined as a 20 dB shift at a single frequency, a 10 dB shift at two adjacent frequencies, or loss of response at three adjacent frequencies. CTCAE grade 1 or greater ototoxicity is defined as a hearing shift of 15-25 dB averaged at 2 contiguous test frequencies.

Using a participant count makes the outcome interpretable as the number of people who experienced a qualifying shift, rather than the number of individual frequency measurements. It is relevant to the stated study question because the monitoring strategies are being compared in terms of hearing shifts detected among participants. The outcome description frames the expected direction as fewer qualifying shifts in COMP-VA, but the posted counts do not follow that expected direction: 15 participants are listed with a shift in COMP-VA and 8 in usual care.

The registry record does not clarify how the two definitions were combined for the primary outcome, whether a participant meeting both definitions was counted once, or how the Program Evaluation 3 wording relates to the stated 35-day timeframe. Those details matter when interpreting exactly which observed events contribute to the endpoint.

7. Results Posted in the Registry

• COMP-VA: 71.4% (15/21) versus 53.3% (8/15) on control; risk difference 18.1 percentage points (95% CI -13.7 to 49.9), risk ratio 1.34 (0.78–2.31); unadjusted two-proportion z-test p = 0.265.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary at the participant level: a participant either has a qualifying ototoxic hearing shift or does not. A common way to compare two groups on a binary endpoint is to estimate each group's event risk and then report a contrast such as a risk difference, risk ratio, or odds ratio. These are different summaries, so their numerical values need not match even when they describe the same underlying comparison. General explanation: a risk difference expresses an absolute separation between group risks; a risk ratio expresses their relative scale; and an odds ratio compares event odds rather than event risks.

What does the risk difference express?

The recalculated risk difference is 0.181 for COMP-VA relative to usual care. A positive value means the observed risk is higher in the first-named arm under that contrast convention. The confidence interval extends from -0.137 to a positive upper limit, so it includes zero. General explanation: when an interval for a risk difference includes zero, the data remain compatible with no group difference as well as with differences on either side of zero. The interval's span also signals limited precision.

The recalculated comparison is unadjusted, meaning it uses the posted group summaries without controlling for other variables. The registry record does not report covariates for an adjusted primary analysis, nor does it establish that the recalculation reproduces the sponsor's full analysis. The sponsor's own reported analyses take precedence for the sponsor's inferential results; their relation to the recalculation is discussed separately.

How should an odds ratio be read?

The registry reports logistic regression, a method often used for binary outcomes. Logistic regression models the log odds of an event and can produce an odds ratio comparing groups. An odds ratio of 1 corresponds to equal odds under the comparison; values above or below 1 indicate higher or lower odds in the first group, depending on the stated reference. The posted regression analyses give odds ratios of 2.2 and 1.4. Their 95% confidence intervals, .55 to 8.8 and .3 to 5.9, respectively, both include 1. The registry does not explain why two regression estimates are reported or what distinguishes their models.

General explanation: odds and risks are related but are not interchangeable. When an outcome is common, an odds ratio can be farther from 1 than the corresponding risk ratio. Thus, the OR should not be read as a direct statement about how many more participants experienced an event. For clinical interpretation, the observed participant counts and an absolute contrast can help complement the regression result.

What does a p-value contribute?

The recalculated unadjusted p-value is 0.265. The sponsor reports p=.27 for one logistic regression analysis and p=.67 for another. A p-value measures how unusual data at least as discrepant as those observed would be under a stated null model and its assumptions. It is not a measure of effect size, a probability that the null hypothesis is true, or a measure of whether a result matters clinically. A larger p-value does not establish equivalence, and a smaller p-value would not by itself establish clinical importance.

General explanation: p-values and confidence intervals are complementary. A confidence interval gives a range of effect estimates compatible with the data and model at its stated confidence level, while a p-value summarizes evidence against a particular null value. Wide intervals can coexist with a non-small p-value when estimates are uncertain. Here, the posted regression intervals are broad, and the recalculated risk-difference interval includes zero.

Why can binary outcomes be difficult to estimate?

Binary outcomes contain less detail than continuous measurements: the endpoint records whether a participant crossed a defined threshold, rather than the magnitude and pattern of every hearing change. The thresholds described in the registry use frequency-specific criteria for ASHA shifts and a change averaged across contiguous test frequencies for CTCAE grade 1 or greater. General explanation: threshold-based outcomes can depend on measurement procedures, timing, and how multiple definitions are combined. The registry record does not clarify the exact combination rule for this primary endpoint.

The listed outcome denominators are limited, and confidence intervals consequently convey substantial uncertainty. General explanation: with relatively little information about events, a few observations can have a strong influence on a group estimate. Logistic regression can also be sensitive to sparse data, especially when the number of events or non-events is limited. The record does not report model diagnostics, variable selection, or other details that would allow evaluation of those issues for the sponsor's regressions.

General explanation: over-dispersion is relevant when data vary more than a model assumes, often in clustered or count settings. The primary outcome is recorded as a participant count with a binary event definition, and no over-dispersion model or diagnostic is reported. It would therefore be inappropriate to infer that such an issue was assessed or that a particular remedy was used.

Randomization supports a group comparison by assigning participants to monitoring strategies, but its interpretation still depends on the integrity of assignment, outcome ascertainment, and follow-up. The registry record identifies randomized allocation but does not report how the sequence was generated or concealed, how missing outcome data were handled, or which analysis population was used. Statistical estimates should be read with those reporting gaps in mind.

10. Confidence Intervals and Precision

The precision of an estimate is reflected by how narrowly its confidence interval constrains plausible values under the analysis model. The recalculated risk difference is 0.181, and its interval has a lower limit of -0.137 and an upper limit above zero. Because the interval crosses zero, the results are compatible with no difference as well as with a difference in either direction. The interval is not narrow enough to identify a single likely magnitude with confidence.

The sponsor's first logistic regression estimate is an odds ratio of 2.2, with a 95% confidence interval from .55 to 8.8. Its second estimate is an odds ratio of 1.4, with a 95% confidence interval from .3 to 5.9. Each interval includes 1 and covers a broad range of possible odds ratios. Those intervals allow both lower and substantially higher odds relative to the comparison value, so the point estimates should not be treated as precise descriptions of the underlying effect.

General explanation: a 95% confidence interval is generated by a method that, under its assumptions, would cover the target parameter in 95% of repeated applications. It does not mean there is a 95% probability that the fixed parameter lies inside this one calculated interval. Its width reflects the information available and the variability assumed by the method.

The listed outcome counts are based on limited arm-specific denominators, which contributes to uncertainty. The record does not explain why the primary outcome denominators differ from the overall enrollment figure, or how participants without a posted outcome were treated. Those reporting gaps make it harder to assess whether the interval reflects all randomized participants. Precision is therefore a property of the stated estimates and models, not a guarantee that all sources of uncertainty have been represented.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculation. The registry record does not report the trial's own sample-size assumptions or justification. These figures are participants per arm, rather than total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a specified fraction of the observed effect as the effect to detect.

For planning for 100% of the observed effect, the illustration gives 112 participants per arm for 80% power and 149 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 204 participants per arm for 80% power and 272 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 467 participants per arm for 80% power and 624 participants per arm for 90% power.

In plain terms, the 80% power column describes the planned number per arm under which the specified effect would be detected by the assumed test in 80% of repeated studies, if the planning assumptions held. The 90% column uses a larger target probability of detecting that effect under the same assumptions. Smaller effects need more participants because they are harder to distinguish from random variation. The associated curve illustrates that planning relationship across the effect assumptions; it is not a report of trial outcomes.

This is not observed power. It is a forward-looking illustration using the observed effect as an input, and should not be interpreted as evidence that the completed trial had a particular chance of finding a result.

12. 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 = 0.533; treatment proportion p₁ = 0.714; average p̄ = 0.624.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6851 = 1.3427.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6730 = 0.5664.
4. n = (1.3427 + 0.5664)² / (0.1810)² = 111.3, rounded up to 112 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 <- 0.533333333333333                          # control proportion
p1 <- 0.714285714285714                          # 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(2099786)
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 = 112 (80% power), 149 (90% power)
 75% of observed effect: n per arm = 204 (80% power), 272 (90% power)
 50% of observed effect: n per arm = 467 (80% power), 624 (90% power)
power.prop.test: 111.3 
Simulated power at n = 112 per arm: 0.803 (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.

13. Analyses Reported by the Sponsor

The registry reports two sponsor logistic regression analyses. One gives an odds ratio of 2.2 with a 95% confidence interval from .55 to 8.8 and p=.27. The other gives an odds ratio of 1.4 with a 95% confidence interval from .3 to 5.9 and p=.67. The record does not explain how these two models differ, which population or covariates each uses, or why both are presented. Their results should therefore be reported as distinct posted analyses rather than treated as interchangeable estimates.

The recalculated comparison is an unadjusted analysis from the posted summary counts. It gives a risk difference of 0.181, a confidence interval with lower limit -0.137 and positive upper limit, and p=0.265. This is not the same effect measure or necessarily the same analysis model as logistic regression. The recalculated result is useful as a transparent summary based on the counts, but it does not replace the sponsor's analysis.

There is no stated discrepancy between the sponsor's analysis and the recalculation. Even so, the sponsor's own analysis takes precedence when describing the sponsor's inferential findings. The registry record does not report enough methodological detail to reconcile the two logistic regression estimates with one another or to establish why their p-values differ. The broad intervals in both sponsor analyses indicate that their estimates are imprecise.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists four outcome measures and five analyses, while reporting no secondary outcomes in the posted results. It includes two logistic regression analyses for the primary comparison, but does not explain why two are reported or whether they represent different models, outcome definitions, populations, or analysis stages. The record does not report a multiplicity adjustment, a prespecified hierarchy of tests, or another method for accounting for multiple comparisons. It is therefore not possible to determine from the record whether the reported p-values were adjusted or how the analyses relate to a prespecified statistical plan.

Multiplicity matters when several outcomes, time points, subgroups, or models are tested. General explanation: conducting more tests can increase the chance that at least one result appears statistically notable by chance, if each test is considered separately. That concern does not establish that the findings are false; it means the number and role of analyses matter when interpreting their evidential weight. The registry record does not provide enough detail to evaluate that issue fully.

The overall enrollment is 47, while the primary outcome arm counts are listed for 21 COMP-VA participants and 15 usual-care participants. The safety figures list 24 and 23 participants at risk in those arms. The registry record does not reconcile these populations or explain which participants contributed to the primary outcome analysis. The outcome denominators may reflect a subset or a particular analysis population, but the reason is not reported in the registry record and should not be inferred.

The registry does not report how missing hearing assessments were handled, whether all randomized participants were analyzed in their assigned groups, or how withdrawals and incomplete follow-up were addressed. It also does not report imputation methods or sensitivity analyses for missing outcomes. These gaps limit evaluation of potential bias from incomplete outcome measurement. No assumption about the direction or extent of missingness is justified from the posted information.

The randomization method and allocation concealment are not described. Although the design is identified as randomized, the record does not report a detailed statistical analysis plan, the prespecified handling of protocol deviations, or whether outcome assessors were masked. The single-masking designation does not identify who was masked. These are reporting limitations, not evidence that any particular procedure was or was not used.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The serious adverse event figures list 0 serious events among 24 participants at risk in COMP-VA and 0 among 23 participants at risk in usual care. The registry also lists 2 deaths in COMP-VA and 4 in usual care. These are separate posted counts; the record does not state that the deaths were caused by the monitoring program, cisplatin, or any other study-related factor.

Zero reported serious events does not establish that serious events could not occur. General explanation: when event counts are sparse, the data provide limited information about the frequency of uncommon outcomes. The record does not report the serious-event definition, event collection procedures, follow-up duration for safety, or whether the death counts are included in another adverse-event category. It also does not provide details about the circumstances or timing of the deaths.

The at-risk counts for safety differ from the primary outcome denominators. The registry record does not explain that difference or describe the safety analysis population. These figures should therefore be read as the reported safety counts, not as a complete account of all possible harms or as a causal comparison. The absence of listed serious events is not evidence that all safety outcomes were assessed or that there were no non-serious events.

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

The results describe a randomized comparison of two hearing-monitoring approaches during cisplatin treatment. In the posted primary outcome counts, 15 COMP-VA participants and 8 usual-care participants had an ototoxic hearing shift. The observed count is higher in COMP-VA, despite the registry description's stated expectation of fewer shifts in that arm. That contrast is descriptive; the estimates do not establish that the monitoring approach caused the observed pattern.

The recalculated risk difference is 0.181, with a confidence interval that includes zero, and the unadjusted p-value is 0.265. The sponsor's logistic regression estimates also have broad 95% confidence intervals that include an odds ratio of 1. The data are therefore not precise enough to determine the direction and magnitude of a group difference with confidence. This does not demonstrate that the strategies are equivalent, nor does it establish that one is superior.

The endpoint is a threshold-defined hearing shift, and the registry record does not clarify exactly how the ASHA and CTCAE criteria were combined for the primary result. It also does not report the analysis population, the handling of missing assessments, or the distinction between the two sponsor regression models. These details affect how the counts and model estimates should be understood.

The posted results do not establish the effect of monitoring on long-term hearing, patient experience, treatment decisions, or functional outcomes. Secondary outcomes are not posted. The safety record lists no serious adverse events in the at-risk groups and reports deaths in both arms, but it does not attribute those deaths or provide enough context to interpret them causally.

The most defensible reading is that the registry reports a higher count of qualifying shifts in COMP-VA than in usual care, alongside uncertain and imprecise comparative estimates. The data do not support a firm conclusion about whether the monitoring strategies differ in their effects on the stated endpoint.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how monitoring frequency and measurement strategy are evaluated when the outcome is a threshold-defined event. A participant-level count is easy to interpret, but it compresses complex hearing measurements into whether a qualifying shift occurred. The outcome definitions include changes at individual or adjacent frequencies and a change averaged across contiguous frequencies. How such criteria are operationalized can shape the event count and, in turn, the estimated group contrast.

The results also illustrate why an observed difference should not be read in isolation. The COMP-VA arm has a larger posted count of participants with shifts, but the estimates have broad uncertainty. The recalculated interval includes zero, and the sponsor's regression intervals include an odds ratio of 1. Statistical interpretation depends on effect estimates and their precision, as well as on a p-value. A count pattern alone does not identify a reliable underlying difference.

Another important issue is the reporting of analysis populations. The overall enrollment, primary outcome denominators, and safety at-risk counts do not match, and the registry record does not explain why. Without knowing which participants were analyzed and how incomplete assessments were treated, readers cannot fully assess the potential impact of missing outcome data.

Finally, the record lists multiple outcomes and analyses but does not explain the relation between the two logistic regression results or describe multiplicity handling. Clear reporting of analysis plans, endpoint construction, and participant flow is especially important when the available group counts are limited. These considerations affect how confidently the posted evidence can be interpreted, independently of whether a monitoring approach is practically useful.

18. Limitations

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

The registry record leaves several trial-specific questions unresolved. Although the study is described as randomized and single masked, it does not identify who was masked, how the random sequence was generated, or whether allocation was concealed. It also does not describe the characteristics of eligible participants or provide detailed inclusion and exclusion criteria. These omissions limit assessment of the design and the population to which the results may apply.

The primary endpoint description names ASHA and CTCAE hearing-shift criteria, but does not explain precisely how they were combined into the participant count or how the Program Evaluation 3 wording relates to the 35 days post-randomization timeframe. The record does not provide the measured hearing data or describe outcome adjudication. The primary outcome denominators also are not reconciled with overall enrollment or the safety at-risk counts.

The two sponsor logistic regression analyses have different estimates and p-values, but the registry does not explain their distinct purposes, models, covariates, or analysis populations. The original statistical analysis plan, sample-size justification, missing-data methods, and multiplicity approach are not reported in the registry record. No conclusion about those unreported procedures should be inferred.

The posted primary outcome is based on a limited number of participants, and the confidence intervals are broad. Four outcome measures and five analyses are listed, but secondary results are not posted. Safety reporting is also limited: serious adverse events and deaths are listed without definitions, timing, attribution, or further clinical context. These limitations constrain both the statistical interpretation and the scope of conclusions that can be drawn from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized Trial Comparison of Ototoxicity Monitoring Programs — NCT02099786.
• Registry record last updated 2019-10-09; status last verified 2019-09.
• Results first posted 2019-10-09.
• 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

The registry record describes NCT02099786, a completed randomized, parallel-group trial of COMP-VA versus usual-care hearing monitoring for Veterans receiving cisplatin. It lists single masking, enrollment of 47, and a primary completion date of 2018-05-05. COMP-VA involved hearing testing at each treatment and at 1 month following treatment; usual care followed Audiology Clinic protocol.

The primary outcome was the number of participants with an ototoxic hearing shift at 35 days post randomization. The posted counts are 15 among 21 COMP-VA participants and 8 among 15 usual-care participants. The recalculated risk difference is 0.181, with a confidence interval including zero; the sponsor reports two logistic regression analyses with broad confidence intervals. The record does not explain the differing analysis populations or the distinction between the regression models.

The registry lists four outcome measures and five analyses, but no secondary outcomes are posted. It reports no serious adverse events in the at-risk groups and lists deaths in both arms without attribution. Important details about the original design assumptions, missing data, multiplicity, and analysis populations are not reported in the registry record.