Safety and Efficacy of RRx-001 in the Attenuation of Oral Mucositis in Patients Receiving Chemoradiation for the Treatment of Oral Cancers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of RRx-001 in the Attenuation of Oral Mucositis in Patients Receiving Chemoradiation for the Treatment of Oral Cancers (NCT03515538), a randomized phase 2 study. The primary outcome is Duration of Severe Oral Mucositis (SOM).

2. Clinical Question

The study was designed to assess safety and efficacy in a phase 2a setting, but the registry record does not report a formal hypothesis or decision rule. The central clinical question is whether the recorded duration of severe mucositis varied with RRx-001 schedule when it was added to chemoradiation. The posted results describe arm-level means and standard deviations, alongside unadjusted comparisons against the pre-treatment-only RRx-001 arm. These results do not, by themselves, establish that any schedule caused a difference. The open-label design and small arm-level outcome counts are relevant when interpreting the observed group patterns.

3. Trial Design

This was a randomized, parallel-group, open-label, multicenter phase 2a study. Its title identifies the population as patients receiving chemoradiation for locally advanced squamous cell carcinoma of the oral cavity or oropharynx. The study was completed, with enrollment of 53. The registry record lists a start date of 2018-07-12 and primary completion on 2019-10-22.

All participants were to receive standard-of-care radiation therapy with cisplatin. The standard-care arm received no RRx-001 and was described as receiving a 7-week course of fractionated radiation with cisplatin administered in a high-dose regimen. The three other arms received RRx-001 during the two weeks before chemoradiation began. One of those arms had no RRx-001 during chemoradiation; another had two additional doses during treatment; and the third had six additional doses during treatment. The schedules therefore differ in whether and how often RRx-001 continued during radiation and cisplatin treatment.

Randomization can help balance participant characteristics across groups, while an open-label design means the treatment assignment was not masked. The registry record does not report details of the randomization procedure, allocation concealment, stratification, or measures to reduce bias in outcome assessment. It also does not report the original sample-size rationale or the planned primary statistical model. These details should not be inferred from the posted group summaries.

The registry lists secondary outcomes that include time to onset of severe oral mucositis, incidence of severe oral mucositis, and opioid use. The primary outcome was duration of severe oral mucositis. Posted arm counts for the primary outcome vary, and the registry record does not explain the relationship between those outcome counts and the total enrollment. Consequently, interpretation should focus on the outcome-specific group summaries rather than assuming that every enrolled participant contributed to every reported measure.

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: All participants: number of days from the start of oral mucositis greater than a grade zero until resolution.

5. Baseline Characteristics

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

Population: Safety Population comprises all subjects who are randomized and received at least 1 dose of study drug and will be used for all analyses of safety. Analysis is based on actual treatment group

6. Primary Endpoint

The registry lists the primary outcome as Duration of Severe Oral Mucositis (SOM), measured over From start of treatment through 28 days post treatment for up to 11 weeks from Start of Treatment.

The primary endpoint was duration of severe oral mucositis, measured in days. The registry defines severe oral mucositis as grade 3 or 4 on the WHO Mucositis Grading Scale. Grade 3 describes oral ulcers with a liquid diet only, and grade 4 describes oral alimentation as impossible. For each participant, the endpoint totals the days spent at grade 3 or 4 during the randomized treatment period. The stated timeframe runs from treatment start through 28 days after treatment, for up to 11 weeks from treatment start.

This endpoint captures duration rather than simply whether severe mucositis occurred. It can therefore reflect both the occurrence and persistence of severe symptoms over the specified observation period. The registry states that higher duration values indicate worse outcomes. The outcome is summarized as a mean and standard deviation for each arm, so the arm mean describes average recorded duration while the standard deviation describes the spread of participant values around that mean.

The registry’s population description also refers to days from the start of oral mucositis above grade zero until resolution, whereas its endpoint description defines the duration as days at grade 3 or 4. The record does not explain this difference in phrasing. Interpretation of the posted primary outcome therefore follows the explicit severe-mucositis definition in the endpoint description, while recognizing the wording difference in the population field.

7. Results Posted in the Registry

• RRx-001 Pre-Treatment, 2 Concurrent Doses Plus SOC: mean 27.70 versus 22.90 on control; difference 4.80 (95% CI -13.44 to 23.04), standardized effect d = 0.23; z-test p = 0.606.
• RRx-001 Pre-Treatment, 6 Concurrent Doses Plus SOC: mean 35.20 versus 22.90 on control; difference 12.30 (95% CI -6.73 to 31.33), standardized effect d = 0.50; z-test p = 0.205.
• Standard of Care: mean 37.80 versus 22.90 on control; difference 14.90 (95% CI -6.24 to 36.04), standardized effect d = 0.61; z-test p = 0.167.

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.

Incidence of Severe Oral Mucositis

• 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:
  • RRx-001 Pre-Treatment, 2 Concurrent Doses Plus SOC: 40.0% (4/10) versus 0.0% (0/12) on control; risk difference 40.0 percentage points (95% CI 9.6 to 70.4); unadjusted two-proportion z-test p = 0.015.
  • RRx-001 Pre-Treatment, 6 Concurrent Doses Plus SOC: 46.2% (6/13) versus 0.0% (0/12) on control; risk difference 46.2 percentage points (95% CI 19.1 to 73.3); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for RRx-001 Pre-Treatment, 2 Concurrent Doses Plus SOC 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 proportion with the event is statistically higher for RRx-001 Pre-Treatment, 6 Concurrent Doses Plus SOC than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the question beyond duration of severe oral mucositis: they include onset, incidence, and opioid use. Together, these outcomes could describe different aspects of the clinical course, but they are not interchangeable. Duration concerns the time spent at severe grades, incidence concerns whether severe mucositis was recorded, onset concerns when it began, and opioid use is a separate measure of supportive treatment. A pattern across these measures would be informative only if their definitions, observation periods, and analyses were interpreted together.

The posted incidence counts vary across the arms, while the registry record contains no reported analysis entries for the secondary outcomes. The incidence comparisons available in the posted data are unadjusted recalculations. They should not be treated as confirmatory evidence or as a replacement for the primary duration outcome. The registry record does not provide results for the other listed secondary outcomes in the information reported for this trial.

Unadjusted secondary results carry less weight because several outcomes and comparisons can create opportunities for chance findings. No multiplicity procedure or hierarchy for interpreting secondary outcomes is reported in the registry record. A nominal p-value from one secondary comparison therefore does not account for the broader set of outcomes that may have been considered. It is also important not to infer consistency or inconsistency across endpoints where results are not posted.

Secondary measures can help contextualize a primary result, but they do not repair limited precision in the primary comparison. Nor can one endpoint establish the pattern in another: a count of participants with severe mucositis does not determine how long severe episodes lasted, and duration does not determine when symptoms first appeared. The overall secondary evidence is incomplete in the registry record, so it supports only a limited account of how these related outcomes were assessed.

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

• Time to Onset of Severe Oral Mucositis
• Incidence of Severe Oral Mucositis
• Opioid Use

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure in the sense that it is summarized by a mean and standard deviation, although each participant’s duration is counted in days. The registry reports the mean for each arm, which represents the average number of severe-mucositis days among participants contributing to that arm’s outcome summary. The standard deviation describes how dispersed individual durations were around that arm mean. It is not a confidence interval for the mean and does not describe the range of all participant outcomes.

What does a mean difference represent?

A mean difference compares the average duration in one arm with the average duration in the reference arm. In the posted comparisons, the reference is RRx-001 pre-treatment plus standard care. A positive reported mean difference therefore indicates a higher average duration in the named comparison arm than in that reference group. Since the endpoint definition states that higher duration is worse, a positive difference points toward more days of severe mucositis in the comparison arm. This is a description of the direction of the estimate; it is not proof that the assigned schedule caused the difference.

The registry comparisons include a confidence interval and an unadjusted p-value. The confidence interval expresses uncertainty in the estimated mean difference under the assumptions of the calculation. Intervals that include zero are compatible with no difference as well as with differences in either direction within the interval. The p-value measures how unusual the observed estimate, or a more extreme one, would be under a specified null model of no difference. It does not give the probability that the null hypothesis is true, and it does not measure clinical importance. The p-values are unadjusted, so they should not be treated as if a multiplicity correction had been applied.

Why does variability matter?

Participant outcomes vary within the arms, as reflected by the reported standard deviations. Greater variability generally makes an arm mean less precise when the number of participants is limited. The observed spread also matters because a mean can conceal different individual patterns: some participants may have shorter durations and others longer durations, even when the average is similar. The registry does not report participant-level distributions, medians, or other summaries that would show the shape of those patterns.

For count outcomes, over-dispersion is a general statistical concern when variability exceeds what a simple count model would expect. If present, over-dispersion can make standard errors too small under an inappropriate model. That is a general consideration, not a claim about the model used in this trial: the registry record does not report a primary analysis model or enough participant-level information to assess over-dispersion. Similarly, the reported summaries do not establish whether the duration distribution was symmetric or whether a normal approximation was suitable for the sponsor’s analysis.

What does an unadjusted recalculation mean?

The posted arm means and standard deviations support simple unadjusted comparisons, which are useful for describing the summaries on a common scale. Such comparisons do not account for baseline characteristics, covariates, missing outcomes, or a prespecified model unless those elements are explicitly part of the analysis. The registry record does not report whether the primary analysis adjusted for any such factors. The unadjusted p-values should therefore be read as descriptive inferential summaries, not as a substitute for a fully specified trial analysis.

Where several schedules or outcomes are examined, testing each contrast can increase the chance of finding at least one apparently notable result by chance. This is the general multiplicity problem. No adjustment for multiple comparisons is identified in the posted primary comparisons, and the registry record does not report a multiplicity plan. The secondary outcomes also lack reported analysis entries. Consequently, isolated unadjusted findings should be interpreted cautiously and in the context of the complete set of outcomes and comparisons, rather than treated as confirmatory evidence.

Random allocation is intended to make groups comparable on average, but it does not guarantee balance in a small trial. Open-label treatment can also influence care, reporting, or outcome assessment, depending on how the outcome is measured. The registry record does not describe blinded assessment of mucositis or other safeguards, so their use cannot be assumed. These design considerations do not invalidate the summaries; they define limits on how confidently a causal interpretation can be made.

Finally, a p-value above a conventional threshold is not evidence of equivalence. Equivalence requires a defined margin and a design and analysis intended to assess whether a difference lies within that margin. The registry record does not report an equivalence or noninferiority framework. The wide intervals around the mean differences are consistent with substantial uncertainty, so absence of a small p-value should not be translated into a conclusion that the schedules are interchangeable.

11. Confidence Intervals and Precision

The confidence intervals around the primary mean differences are wide. For the two-concurrent-dose schedule compared with pre-treatment-only RRx-001, the interval extends from -13.44 to 23.04 days. For the six-concurrent-dose schedule, it extends from -6.73 to 31.33 days. For standard care, it extends from -6.242 to 36.04 days. All three intervals include zero, so the posted estimates do not distinguish clearly between a shorter duration, no difference, and a longer duration relative to the reference group.

These intervals describe uncertainty in the estimated group differences, not the range of individual participant durations. Their width reflects the limited precision of these comparisons, alongside the variability in the observed outcome. The arm standard deviations are 19.08, 23.72, 28.83, and 29.33 days, while the outcome group sizes are 12, 10, 13, and 10. The comparatively large spreads and modest group sizes are important context for interpreting the interval estimates.

A confidence interval is not a guarantee that the true value lies within the interval, nor does it assign probabilities to particular values after the data have been observed. Under the calculation’s assumptions, it provides a range of values reasonably compatible with the observed data at the stated confidence level. The registry record does not report the sponsor’s primary analysis method or its own confidence intervals. The intervals accompanying the posted comparisons should therefore be understood as unadjusted summaries rather than a complete account of the planned analysis.

The intervals also do not resolve the clinical importance of possible differences. The registry record does not report a threshold defining a clinically important difference in days. The estimates and their uncertainty can be described statistically, but a clinical interpretation of how large a difference matters cannot be established from these data alone.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the original trial’s design justification. The registry record does not report the trial’s original sample-size assumptions, target power, or effect size used in planning. The displayed planning estimates use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider effects equal to the observed effect and fractions of that observed effect. For these non-time-to-event comparisons, the estimates are participants per arm, not total participants across both arms. The general convention for time-to-event planning figures would be total events, but the primary outcome is not time-to-event.

The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated planning assumptions, if that effect were the true one. The 90% power column gives the corresponding estimate for a 90% chance. These are design probabilities under assumptions, not probabilities that the treatment works. For a given outcome variability and significance level, planning for a smaller effect requires more participants than planning for a larger effect. The estimates are sensitive to the effect chosen: using a fraction of the observed effect leads to larger required group sizes than using the full observed effect.

These figures are not observed power. They do not describe the probability that this completed trial detected an effect, and they do not change the uncertainty in its observed estimates. In particular, the observed effect may itself be an unstable basis for planning, especially when outcome groups are small. The registry record does not establish whether the planning method matches the assumptions or statistical procedures used in the original trial design. Treat the numbers as conditional illustrations for future planning, not as evidence about the adequacy or success of this trial.

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 = 4.800; pooled standard deviation σ = 21.293.
2. n = 2 × (1.96 + 0.842)² × 21.293² / 4.800² = 308.9, rounded up to 309 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 <- 4.8                      # observed difference in means
sigma <- 21.2934919635085                     # 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(3515538)
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 = 309 (80% power), 414 (90% power)
 75% of observed effect: n per arm = 550 (80% power), 736 (90% power)
 50% of observed effect: n per arm = 1,236 (80% power), 1,655 (90% power)
power.t.test: 309.9 
Simulated power at n = 309 per arm: 0.799 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators examine more than one comparison or outcome. Even when each individual test uses the same significance threshold, the chance of at least one result appearing notable by chance can increase across a collection of tests. This trial has several treatment arms and multiple listed outcomes, so a prespecified approach to controlling or interpreting multiplicity would be relevant to confirmatory claims. The registry record does not report a multiplicity strategy, testing hierarchy, or adjustment for the posted unadjusted comparisons. It is therefore not possible to determine from the record whether the primary comparison was intended to be one of several confirmatory tests or whether the secondary outcomes were exploratory.

The registry record does not report the primary analysis population, such as whether the primary analysis followed all randomized participants according to assigned group. It also does not report how missing outcome observations, withdrawals, protocol deviations, or treatment discontinuations were handled. The primary outcome group counts are listed by arm, but the record does not explain why those counts differ from total enrollment or whether any observations were excluded from a particular summary. No missing-data assumptions, imputation procedures, or sensitivity analyses are reported.

These omissions matter because duration depends on observation over time. If participants have incomplete follow-up, their recorded duration could differ from the duration that would have been observed with complete follow-up. The extent and direction of any such effect cannot be determined without information on missingness and the analysis approach. It would be inappropriate to assume either that no data were missing or that a particular correction was used.

The registry record also does not report the planned model, covariate adjustments, handling of multiple comparisons, or a formal statistical analysis plan. Those items should not be inferred from the posted means, standard deviations, and unadjusted comparisons. The practical consequence is that the reported summaries can be described, but the extent to which they match the trial’s planned confirmatory analysis is not reported in the registry record.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute kidney injury (27.3%), atrial fibrillation (10.0%), nausea (10.0%), vomiting (10.0%), lung infection (10.0%).

The registry lists serious adverse event counts alongside the number at risk in each arm. Serious adverse events were reported for 4 of 12 participants in the RRx-001 pre-treatment plus standard-care arm, 4 of 11 in the two-concurrent-dose arm, 6 of 13 in the six-concurrent-dose arm, and 5 of 10 in the standard-care arm. These counts are descriptive. They do not establish that an event was caused by RRx-001, cisplatin, radiation, or the underlying illness, and they do not support a causal comparison among the arms.

The record also lists one death in the six-concurrent-dose arm and no deaths in the other arms. The registry’s listed serious adverse event terms include acute kidney injury, atrial fibrillation, nausea, vomiting, lung infection, and hypophosphataemia, with their listed percentages. The record does not provide enough context in these summaries to attribute those terms to a particular treatment schedule or to interpret them as comparative risks. Serious adverse event counts should be considered alongside the small group sizes and the broader clinical context; the registry entries alone do not establish a safety profile.

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

The posted results describe a small randomized study of RRx-001 schedules added to cisplatin and radiation. For the primary outcome, the mean duration of severe oral mucositis was lowest in the pre-treatment-only RRx-001 arm, and the other arm means were higher. The reported unadjusted comparisons against that reference have confidence intervals that include zero and span a wide range of possible differences. The data therefore show a descriptive ordering of arm means, but they do not provide a precise estimate of how the schedules differ.

These findings do not establish that RRx-001 reduces or increases severe mucositis duration. They also do not establish that the schedules are equivalent, or that a result for one schedule applies to another. The comparisons are relative to the pre-treatment-only arm, not direct inferential comparisons between every active schedule and standard care. The registry record does not report a clinically important difference threshold or an equivalence framework.

General statistical interpretation distinguishes absence of clear evidence from evidence of no effect. Wide intervals and non-small unadjusted p-values leave uncertainty; they are not proof that all plausible differences are unimportant. Equally, the ordering of observed means alone is not proof of a treatment effect. Randomization supports comparisons in principle, but small groups, variability, open-label conduct, and incomplete reporting of analysis details limit how far these summaries can be extended.

The results apply to the participants and treatment schedules recorded in this study. They should not be taken as a treatment recommendation or as a forecast for a different patient population. The record’s limited reporting of missing-data handling, analysis populations, multiplicity, and the planned model further constrains interpretation. A complete clinical judgment would require evidence beyond these posted group summaries.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its question involves several active schedules and a standard-care group, while the posted primary comparisons use one RRx-001 schedule as the reference. The reference choice changes the meaning of each estimate: the reported differences describe contrast with pre-treatment-only RRx-001, not a direct test of each schedule against standard care. This distinction is essential when reading a multi-arm study.

The outcome is duration in days, but the group summaries show substantial within-arm variability and limited outcome counts. In that setting, differences between means can be unstable, and confidence intervals communicate uncertainty that a simple rank ordering of averages can obscure. The interval estimates are especially useful for preventing a non-significant result from being misread as proof of no difference.

The trial also illustrates why the distinction between a posted result and a planning calculation matters. The sample-size illustrations are based on observed effects and stated planning assumptions; they do not reveal the original rationale or the trial’s observed probability of detecting an effect. Planning estimates can help frame what a future study might require under chosen assumptions, but they are not a retrospective quality score.

Finally, this record underscores the importance of reporting analysis populations, missing-data handling, multiplicity plans, and the primary model. Without those details, readers can describe the group summaries and their uncertainty, but they cannot fully evaluate how closely the reported analyses followed the intended design. Statistical transparency is part of interpreting both positive and inconclusive results.

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 are specific to interpreting this trial’s posted record. The open-label design means treatment assignment was known, and the registry record does not report whether mucositis grading was assessed by blinded evaluators. Because the primary outcome depends on grading severity, the absence of reported assessment procedures limits evaluation of possible observer or reporting influences.

The study has four arms, but outcome counts are modest and differ by arm. The record does not explain the relationship between those outcome counts and enrollment of 53, or whether exclusions, withdrawals, or incomplete follow-up account for the difference. It also does not report how missing primary outcome data were handled. These omissions limit assessment of whether the group summaries represent comparable analysis populations.

Only selected primary contrasts are posted, with the pre-treatment-only RRx-001 group as reference. Direct analyses between the other RRx-001 schedules and standard care are not reported in the record. The registry also does not report a prespecified multiplicity plan, primary analysis model, clinically important difference, or original sample-size justification. Those gaps make it difficult to assess whether the displayed inferential results match the intended trial analysis.

The endpoint definition is framed as days at grade 3 or 4, while the population description uses wording about days from oral mucositis above grade zero until resolution. The registry does not clarify that difference. The secondary outcomes are incompletely reported, with no reported analysis entries for the available secondary outcomes. These reporting limitations do not erase the posted results, but they narrow the conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of RRx-001 in the Attenuation of Oral Mucositis in Patients Receiving Chemoradiation for the Treatment of Oral Cancers — NCT03515538.
• Registry record last updated 2024-11-04; status last verified 2024-10.
• Results first posted 2024-11-04.
• 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

NCT03515538 was a completed, randomized, parallel-group, open-label phase 2a study with enrollment of 53. It assessed RRx-001 added to cisplatin and radiation for patients receiving chemoradiation for oral cancers. The RRx-001 arms differed by whether doses were given only before chemoradiation or also during treatment; the comparator received standard care without RRx-001.

The primary outcome was duration of severe oral mucositis in days, defined as days at WHO grade 3 or 4. The lowest posted arm mean was in the RRx-001 pre-treatment-only group. Reported unadjusted comparisons against that group had wide confidence intervals that included zero. The record does not report the original sample-size rationale, primary analysis model, missing-data handling, or multiplicity plan. The results are descriptive and imprecise, and the record does not establish a causal or clinically definitive difference among schedules.