Doxepin Hydrochloride in Treating Oral Mucositis Pain in Patients With Head and Neck Cancer Undergoing Radiation Therapy With or Without Chemotherapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Doxepin Hydrochloride in Treating Oral Mucositis Pain in Patients With Head and Neck Cancer Undergoing Radiation Therapy With or Without Chemotherapy (NCT01156142), a randomized phase 3 study. The primary outcome is Total Pain Reduction (Mouth and Throat).

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, phase III crossover trial sponsored by the Alliance for Clinical Trials in Oncology. It enrolled 155 participants with head and neck cancer receiving radiation therapy, with or without chemotherapy. The registry lists oral mucositis and pain among the conditions addressed. The trial compared doxepin hydrochloride oral rinse with placebo.

Participants were assigned to one of two treatment sequences. In the doxepin-placebo sequence, participants received doxepin on day 1 and could cross over to placebo on day 2. In the placebo-doxepin sequence, participants received placebo on day 1 and could cross over to doxepin on day 2. Both treatments were rinsed, gargled, and spat out over 1 minute. The study was double-blind, meaning the design masked treatment assignment as recorded by the registry; further details about how masking was maintained are not reported in the registry record.

The primary analysis was restricted to primary data from the first phase, rather than combining observations across both treatment periods. The primary outcome analysis included 69 participants in the doxepin-placebo group and 71 in the placebo-doxepin group. These analysis counts are not the same as the enrollment total; the reasons for each participant’s inclusion or exclusion are not fully reported in the registry record.

The registry record marks the trial completed. It does not report the original sample-size justification, the planned duration of recruitment, or the detailed procedures for sequence generation and allocation concealment. The record describes the primary test and confidence interval, but the full statistical analysis plan is not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: If a patient cancels, is missing baseline data, or only provides baseline data, he/she will be excluded from the statistical analysis. The primary analysis of the total pain reduction will only use primary data from the first phase.

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 Total Pain Reduction (Mouth and Throat), measured over Baseline and Day 1.

The primary endpoint was total pain reduction for the mouth and throat, measured in units on a scale. Pain was recorded on an 11-point numerical scale, from 0 for no pain to 10 for the worst pain imaginable or possible. The endpoint combined mouth and throat ratings by taking their average and calculating an area under the curve, with baseline adjustment.

Instead of using the raw time scale, the area-under-the-curve calculation used numerical time weights of 1, 2, 3, 4, 5, and 6. The registry explains that this weighting was intended to give appropriate weight to patient-reported pain outcomes soon after treatment. For terminal missing observations, the area was calculated by proration; for intermittent missing observations, simple imputation was used.

An area-under-the-curve endpoint condenses repeated measurements into a single measure reflecting the pattern of recorded pain over the assessment period. Baseline adjustment is intended to account for starting pain levels when comparing the groups. These features make the endpoint a summary of pain ratings over time rather than a single rating at one assessment. The primary analysis used only first-phase data. The registry record does not report the exact assessment schedule or the numerical definition of the adjustment beyond the description of the calculation.

7. Results Posted in the Registry

• Arm II (Placebo-Doxepin): mean -4.70 versus -9.10 on control; difference 4.40 (95% CI 2.06 to 6.74), standardized effect d = 0.62; z-test p = <0.001.

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.

Total Taste of the Oral Rinse

• 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:
  • Arm II (Placebo-Doxepin): mean 5.10 versus 7.70 on control; difference -2.60 (95% CI -5.05 to -0.15), standardized effect d = -0.35; z-test p = 0.038.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Arm II (Placebo-Doxepin) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Total Stinging or Burning From the Oral Rinse

• 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:
  • Arm II (Placebo-Doxepin): mean 4.00 versus 9.60 on control; difference -5.60 (95% CI -8.32 to -2.88), standardized effect d = -0.68; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Arm II (Placebo-Doxepin) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Total Drowsiness Increase

• 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:
  • Arm II (Placebo-Doxepin): mean -2.40 versus -0.70 on control; difference -1.70 (95% CI -4.57 to 1.17), standardized effect d = -0.20; z-test p = 0.246.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm II (Placebo-Doxepin) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several aspects of the oral rinse and the treatment experience: taste, stinging or burning, drowsiness, use of alternative analgesics, and preference for continuing oral doxepin. The posted numerical comparisons include taste, stinging or burning, and drowsiness. Results for alternative analgesic use and treatment preference are not reported in the registry record, although those outcomes are listed as secondary measures.

Across the secondary measures with numerical results, the posted summaries suggest that group differences were not uniform across every aspect of the experience. The reported contrasts for taste and stinging or burning differ from the pattern for drowsiness, for which the simple mean-based recalculation does not provide a clear separation. This broader pattern does not add a second primary endpoint: these outcomes address different questions from the primary pain-reduction measure.

Secondary findings can help describe the range of measured outcomes, but they generally carry less weight than a prespecified primary result. When several outcomes are tested, the chance of seeing at least one apparently unusual result by chance can increase. General statistical practice may address this through multiplicity adjustment or by treating secondary analyses as exploratory. Whether an adjustment was planned or applied is not reported in the registry record. The unadjusted secondary p-values should therefore be read cautiously rather than as a set of independent confirmations.

The registry record reports some differences between the sponsor’s rank-based tests and the simple mean-based recalculations. These analyses use different statistical approaches, and their estimates or p-values need not agree exactly. The record does not supply enough methodological detail to resolve all such differences. Taken together, the secondary results provide context about measured experiences, but they do not replace or independently establish the primary result.

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

• Total Taste of the Oral Rinse
• Total Stinging or Burning From the Oral Rinse
• Total Drowsiness Increase
• Incidence of Using Alternative Analgesics Between 2 and 4 Hours After the Initial Mouthwash
• Patient Preference for Continuing Therapy With Oral Doxepin Hydrochloride

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint was continuous: it was reported as a mean with a standard deviation. A continuous outcome can take values across a numerical scale, rather than being limited to categories such as yes or no. The registry reports group means of -9.1 and -4.7 units, with standard deviations of 7.9 and 6.1, respectively. The standard deviation describes the spread of participant values around each group mean. It is not a confidence interval and does not directly describe the precision of the difference between groups.

The endpoint was constructed from repeated pain ratings. Mouth and throat ratings were averaged, adjusted for baseline, and summarized as an area under the curve using numerical weights of 1 through 6. The registry says terminal missing data were handled by proration and intermittent missing data by simple imputation. These rules determine how some incomplete observations contributed to the summary. The registry does not report how many observations were missing, how often each method was used, or sensitivity analyses under other missing-data assumptions.

What does the reported rank-based test assess?

The sponsor’s reported method was the Wilcoxon rank-sum test, also called the Mann-Whitney test. In general, this test compares the ordering of observations between two groups by using ranks rather than directly testing a difference between arithmetic means. It can be useful when the analysis is intended to rely less on a particular distributional shape than a conventional mean-based test. A rank-based test does not automatically estimate a difference in means; the registry nevertheless labels the reported parameter as a mean difference in final values. The record does not provide further detail about the relationship between the test statistic and the reported estimate.

The posted sponsor result is a mean difference of -4.4, with a 95% confidence interval from -6.7 to -2.1 and p < 0.001. The group-order convention matters for the sign: reversing the subtraction reverses the sign, without changing the magnitude of the contrast. The reported analysis and its confidence interval are the sponsor’s results. A separate simple recalculation from the group summaries gives a mean difference of 4.4 in the opposite group order, with a 95% confidence interval from 2.057 to 6.743 and p < 0.001.

What is the recalculation, and what is it not?

The recalculation is an unadjusted comparison based on the posted summary statistics. It does not reproduce the rank-based test, the baseline-adjustment procedure, or any participant-level analysis. In general, reconstructing an estimate from group summaries is less informative about the underlying data than an analysis of individual observations. It is best read as a secondary numerical check, not as a replacement for the sponsor’s own analysis. The registry record does not report participant-level data that would allow independent reproduction of the analysis.

General statistical interpretation distinguishes an estimate from a test. The estimate describes the direction and size of a contrast on the endpoint scale; a confidence interval conveys uncertainty around that estimate; and a p-value assesses compatibility with a specified null model under the test’s assumptions. These quantities answer related but different questions. A small p-value is not a measure of clinical importance, and a confidence interval does not guarantee that the true value lies within its limits.

Why can variability matter?

Standard deviations describe variability among participants. General statistical reasoning says that greater variability can make a group contrast less precisely estimated when other design features are held fixed. This is one reason that an observed difference should be read together with its uncertainty, rather than judged from group means alone. The registry reports standard deviations for the continuous outcomes but does not report distribution plots or other diagnostics for the primary outcome.

The trial used a crossover sequence, but the primary analysis used only the first phase. This means the primary comparison is between the randomized groups in that first phase; it is not the paired within-person comparison that might be formed from both periods. In general, crossover designs can use within-person comparisons to account for stable participant characteristics, but that general property does not describe the primary analysis. The registry record does not report a crossover analysis using both phases for the primary outcome, or details about any period or carryover assessment.

The confidence interval and p-value should also be interpreted in the context of the analysis population. The registry specifies exclusions for cancellation, missing baseline data, or baseline-only data, and states that the primary analysis used first-phase data. It does not report the complete flow of participants through those criteria or whether additional analysis populations were used. Consequently, the extent to which missingness or exclusions could affect the estimated contrast cannot be determined from the registry record alone.

11. Confidence Intervals and Precision

The sponsor’s primary analysis reports a 95% confidence interval from -6.7 to -2.1 for its mean difference of -4.4. This interval describes uncertainty in the estimated contrast under the reported analysis. Because its endpoints are on the same scale as the estimate, it also conveys the range of effect values compatible with the analysis, subject to the method’s assumptions. The interval excludes zero, consistent with the reported p-value of p < 0.001 for the primary comparison.

The simple recalculation uses the reverse group order and gives a mean difference of 4.4, with a 95% confidence interval from 2.057 to 6.743. The opposite signs reflect the group order rather than two different magnitudes of contrast. This recalculated interval is not the sponsor’s rank-based interval; it comes from an unadjusted calculation using posted summary statistics. The registry’s reported analysis takes priority as the trial’s own result.

In general, a confidence interval is not a guarantee that the true value is inside its limits. It is a method for expressing the uncertainty that would arise from repeated use of the same procedure under its assumptions. A narrower interval indicates greater precision than a wider interval on the same scale, but precision does not establish that the estimate is unbiased or clinically important.

The registry does not report a clinical threshold for interpreting the size of the primary contrast. It therefore does not establish whether any particular value within the interval would be considered important to patients or clinicians. The interval quantifies statistical uncertainty in the posted estimate, not the certainty of benefit, the chance that a participant will experience a particular outcome, or the likelihood that another trial would produce the same result.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are participants per arm, not total events. They are planning illustrations computed from the observed effect, not the trial’s original design assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original sample-size justification is not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 41 participants per arm for 80% power and 54 participants per arm for 90% power. Planning for 75% of the observed effect gives 72 participants per arm for 80% power and 96 participants per arm for 90% power. Planning for 50% of the observed effect gives 161 participants per arm for 80% power and 216 participants per arm for 90% power.

In general, power is the probability that a planned study will detect an effect of a specified size under the design assumptions, if that effect is present. The 80% and 90% columns therefore represent different planning targets: the higher target generally calls for more participants for the same assumed effect. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. The figures are illustrations based on this trial’s observed estimate; they do not describe the power achieved by the completed trial. This is not observed power.

The illustrations depend on the observed effect, which is itself uncertain. They should not be treated as a definitive recommendation for a future study or as evidence that the original trial was designed around these assumptions. The registry does not report the trial’s original assumptions, nor does this planning calculation account for details beyond the stated assumptions.

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 = 4.400; pooled standard deviation σ = 7.045.
2. n = 2 × (1.96 + 0.842)² × 7.045² / 4.400² = 40.2, rounded up to 41 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 <- 4.4                      # observed difference in means
sigma <- 7.04467112818958                     # 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(1156142)
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 = 41 (80% power), 54 (90% power)
 75% of observed effect: n per arm = 72 (80% power), 96 (90% power)
 50% of observed effect: n per arm = 161 (80% power), 216 (90% power)
power.t.test: 41.2 
Simulated power at n = 41 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s own primary analysis used the Wilcoxon rank-sum test and reported a mean difference of -4.4, with a 95% confidence interval from -6.7 to -2.1 and p < 0.001. The simple recalculation uses the posted group means and standard deviations and gives 4.4, with a 95% confidence interval from 2.057 to 6.743 and p < 0.001. The contrast is expressed in the reverse group order in the recalculation, so the sign is reversed. The primary results are not marked as discrepant.

The recalculation is unadjusted and based on summary statistics; it does not recreate the sponsor’s rank-based method or use participant-level observations. It is therefore a numerical cross-check, not a competing trial analysis. The sponsor’s reported analysis is the appropriate reference for what the registry records as the trial’s own primary result.

For secondary outcomes, the posted sponsor analyses also use the Wilcoxon (Mann-Whitney) method, while the simple recalculations are mean-based. Differences between p-values or confidence intervals can arise because the methods and estimands are not identical. The registry does not describe all details needed to reproduce those analyses or explain every difference between the reported tests and the summary-statistic calculations.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and lists secondary outcomes, but whether the analysis plan adjusted for multiple comparisons is not reported in the registry record. Multiplicity matters because testing several outcomes can increase the chance of at least one nominally notable result even when none reflects a real difference. Without a reported adjustment strategy or a clear hierarchy among secondary outcomes, the secondary p-values should not be treated as though each were the sole planned test.

The registry describes specific procedures for missing values in the primary area-under-the-curve calculation: terminal missing data were handled by proration, while intermittent missing data were handled by simple imputation. It also states that participants who cancelled, lacked baseline data, or had baseline data only were excluded from the primary statistical analysis. The primary analysis used data from the first phase only. How many participants met each exclusion criterion, how much outcome data were missing, and whether missingness differed by randomized group are not reported in the registry record.

In general, imputation fills in missing values according to an assumed rule, and conclusions can depend on whether that rule is appropriate. Proration and simple imputation are the approaches named in the record, but the registry does not provide enough detail to assess their implementation or the sensitivity of results to alternative assumptions. No additional missing-data sensitivity analyses are reported in the registry record.

The analysis population is described only for the primary endpoint at a broad level. The record does not report whether an intention-to-treat population, a per-protocol population, or other analysis sets were defined, nor does it give a full participant flow by treatment sequence. Interim analyses and stopping rules are not reported in the registry record. These absences limit assessment of how analysis choices, missingness, or repeated testing may have influenced the posted findings.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The serious adverse event figures are reported by sequence group. In the doxepin-placebo group, 0 serious adverse events were reported among 74 participants at risk. In the placebo-doxepin group, 0 serious adverse events were reported among 75 participants at risk. These are the posted counts for the groups and the corresponding at-risk denominators; they do not establish that no serious events occurred outside the registry’s recorded scope.

The registry also reports 10 other adverse events among 74 participants at risk in the doxepin-placebo group and 8 among 75 participants at risk in the placebo-doxepin group. These counts should be read separately from the serious adverse event counts. The registry record does not provide further detail in these figures about event types, severity, timing, or whether an event was considered related to treatment. Serious adverse event terms are not listed, and deaths are not reported in the registry record.

Because the trial used a crossover sequence, the group labels refer to treatment order, not a simple summary of all exposure to each treatment. The registry figures alone do not support a full causal comparison of safety between doxepin and placebo. They also do not establish that the treatments are equally safe; the counts are descriptive and should be interpreted with the available reporting limitations in mind.

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

The primary result is a comparison of a defined pain-reduction summary between randomized first-phase groups in a double-blind crossover trial. The sponsor reported a mean difference of -4.4, with a 95% confidence interval from -6.7 to -2.1 and p < 0.001. The simple summary-statistic recalculation expresses the same contrast in reverse order as 4.4, with a 95% confidence interval from 2.057 to 6.743. The signs depend on group order, and the endpoint’s coding should be considered when interpreting direction.

These findings do not by themselves establish the clinical importance of the observed contrast. The registry record does not report a threshold for a meaningful change on this area-under-the-curve measure. Nor does a small p-value establish that a particular participant would experience a particular amount of pain reduction. Statistical evidence about a group contrast and individual experience are different things.

The result applies to the outcome definition and analysis reported: mouth and throat pain were averaged, baseline-adjusted, and summarized using specified numerical time weights, with the primary analysis restricted to the first phase. It should not be automatically generalized to different pain measures, different treatment schedules, or patient groups beyond those described in the registry record. The record does not provide detailed information about all eligibility criteria or the broader clinical context needed to assess such generalization.

The trial’s posted results also include secondary measures and adverse event counts, but these address distinct aspects of the treatment experience and have their own limitations. The registry record does not report multiplicity adjustment for secondary comparisons or a complete account of missing observations and analysis populations. Those omissions matter when judging how much weight to place on secondary findings.

In general, clinical interpretation combines the estimated effect, its uncertainty, the quality and relevance of the measurement, and the study’s design and limitations. The confidence interval indicates statistical precision under the analysis assumptions; it does not prove a benefit, rule out bias, or settle questions not measured by the trial. The appropriate reading is therefore a trial-specific statistical result, with direction interpreted according to the reported contrast and outcome coding.

18. Why This Trial Matters Statistically

This trial raises several statistical issues that are common in clinical research. First, a crossover design can generate within-participant comparisons, but the primary analysis reported in the registry used only first-phase data. That distinction changes what the estimate represents: the posted primary contrast is between randomized sequence groups in the first phase, not a combined analysis of both treatment periods.

Second, the primary outcome compresses repeated pain ratings into an area-under-the-curve measure. The endpoint’s construction—including averaging mouth and throat ratings, baseline adjustment, numerical weighting of assessment times, and handling of missing values—shapes the result being compared. Transparent reporting of those choices helps readers understand what the numerical estimate means and what it does not capture.

Third, the registry reports a rank-based test alongside a mean-difference parameter. A test based on ranks and a simple mean-based recalculation are related to the same group comparison but are not interchangeable procedures. Reading the estimate, confidence interval, and p-value together makes clear that statistical significance is not the same as precision or clinical importance.

Finally, secondary endpoints and safety counts broaden the descriptive picture, but they do not all answer the primary question. The absence of reported multiplicity procedures, fuller missing-data details, and the original sample-size justification limits how completely readers can assess the full analysis strategy. These are not reasons to discard the posted findings; they identify what the registry record does and does not allow readers to evaluate.

19. Limitations

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

The primary analysis used only first-phase data, although the trial was designed as a crossover. The registry record does not report a primary analysis combining both phases, a period-effect assessment, or a carryover assessment. The first-phase result therefore cannot be interpreted as a full within-participant crossover estimate.

The primary endpoint is a constructed summary rather than a single pain rating. Its calculation uses baseline adjustment, an average of mouth and throat ratings, numerical time weights, and specified approaches to missing observations. The registry record does not report the exact assessment schedule, the amount of missing data, the number of values handled by each missing-data method, or sensitivity analyses. The influence of those choices cannot be assessed from the posted information alone.

The record identifies exclusions for cancellation, absent baseline data, and baseline-only data, but does not provide a complete participant flow or explain all differences between enrollment, analysis, and adverse-event denominators. Additional analysis populations and the detailed statistical analysis plan are not reported in the registry record. The original sample-size justification and any interim analyses are also not reported.

Secondary outcomes include experience measures and treatment-use questions, but numerical results are not reported for every listed outcome. Multiplicity handling is not reported in the registry record, so secondary p-values should not be treated as a family of fully adjusted confirmatory tests. Some secondary sponsor analyses and simple recalculations use different statistical methods, and the record does not give all details needed to reproduce them.

Safety reporting is limited in the available figures. The registry reports serious and other adverse event counts by treatment sequence, but detailed event descriptions, treatment attribution, and deaths are not reported in the registry record. These limitations constrain interpretation of safety and generalization beyond the trial’s described population and treatment schedule.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Doxepin Hydrochloride in Treating Oral Mucositis Pain in Patients With Head and Neck Cancer Undergoing Radiation Therapy With or Without Chemotherapy — NCT01156142.
• Registry record last updated 2017-08-09; status last verified 2017-07.
• Results first posted 2017-05-08.
• 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 record describes a completed, randomized, double-blind phase III crossover trial of doxepin hydrochloride oral rinse versus placebo for acute oral mucositis pain in patients with head and neck cancer receiving radiation therapy, with or without chemotherapy. Enrollment was 155. Participants received one rinse on day 1 and could cross over to the other treatment on day 2.

The primary outcome was baseline-adjusted total pain reduction for mouth and throat, summarized as an area under the curve. The primary analysis used first-phase data and a Wilcoxon rank-sum comparison. The sponsor reported a mean difference of -4.4, a 95% confidence interval from -6.7 to -2.1, and p < 0.001. The registry also reports secondary measures and adverse event counts, with limitations in the detail available for missing data, multiplicity, and the full analysis plan.