Efficacy Study of Dextromethorphan to Treat Rheumatoid Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy Study of Dextromethorphan to Treat Rheumatoid Arthritis (NCT02368093), a randomized na study. The primary outcome is Good European League Against Rheumatism (EULAR) Therapeutic Response Rate.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, placebo-controlled trial of dextromethorphan hydrobromide for rheumatoid arthritis. Participants were assigned to receive either dextromethorphan or placebo as add-on therapy to traditional disease-modifying anti-rheumatic drugs (DMARDs). The study summary describes a 6-month treatment period, and the primary endpoint is assessed at 6 months.

The study is listed as quadruple masked. The registry does not identify which specific groups of people were masked, so the masking label cannot be expanded into more detail. The allocation is recorded as randomized, but the method used to generate or conceal the allocation is not reported in the registry record. The trial phase is recorded as NA.

The registry reports enrollment of 48 participants. The posted endpoint counts are based on 24 participants in the dextromethorphan arm and 24 in the placebo arm. The sponsor is Taichung Veterans General Hospital. The study start is recorded as 2010-01, primary completion as 2012-09, and status as completed.

Details such as eligibility criteria, recruitment sites, the allocation procedure, adherence, treatment discontinuation, and the number included in the endpoint analysis are not reported in the registry record. The record also does not describe a prespecified statistical analysis plan or the trial's original sample-size assumptions. Those absences limit how fully the conduct and analysis can be evaluated from the registry information alone.

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 Good European League Against Rheumatism (EULAR) Therapeutic Response Rate, measured over 6 months.

The primary endpoint is the Good European League Against Rheumatism (EULAR) Therapeutic Response Rate at 6 months. It is recorded as a number of participants: six in the dextromethorphan arm and four in the placebo arm. This endpoint therefore represents a binary outcome at the participant level: each participant either met the good-response definition or did not.

In general, a response endpoint can make a result easier to interpret than a change score alone because it expresses how many participants crossed a defined response threshold. That interpretation depends on having a clear and consistently applied definition of response. The registry record names the EULAR response category but does not give the detailed criteria used to classify a good response, nor does it report who assessed the outcome or whether assessment procedures were standardized.

The endpoint is relevant to the study's stated question about therapeutic response, but it captures only one aspect of rheumatoid arthritis outcomes at one stated follow-up time. It does not, by itself, describe the size of each participant's change, the course of symptoms over time, or other clinical outcomes. No secondary outcome measures are posted in the registry record.

7. Results Posted in the Registry

• Dextromethorphan Hydrobromide: 25.0% (6/24) versus 16.7% (4/24) on control; risk difference 8.3 percentage points (95% CI -14.5 to 31.2), risk ratio 1.50 (0.48–4.65); unadjusted two-proportion z-test p = 0.477.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a risk difference describe?

The risk difference subtracts the event proportion in one arm from the event proportion in the other. For this endpoint, the posted comparison gives a risk difference of 0.083, with the dextromethorphan arm as the arm of interest and placebo as the comparator. A positive value means the observed proportion was higher in the dextromethorphan arm; a negative value would mean it was lower. The value is an absolute contrast between proportions, rather than a relative comparison.

In general, absolute contrasts can be useful because they express how far apart the observed event rates are on the probability scale. Their interpretation depends on the event definition, the population included in each arm, and the follow-up time. Here, the endpoint is a good EULAR response at 6 months. The registry record does not provide a detailed response definition or identify the analysis population beyond the arm counts.

How do the risk ratio and odds ratio differ?

The risk ratio compares the event proportion in one arm with the event proportion in the comparator arm. The odds ratio instead compares the event odds between arms. Both measures describe relative contrasts, but they are not interchangeable, and their numerical values need not be similar. The posted risk ratio is 1.5 and the posted odds ratio is 1.667. Each has a confidence interval that includes its no-association value of one.

In general, relative measures can help describe how outcome frequencies compare proportionally, while the risk difference expresses an absolute separation. None of these measures removes uncertainty in the underlying counts. When event counts are limited, estimates can be imprecise, as reflected by broad confidence intervals. The estimates also depend on the endpoint and the population represented by the data.

What does the p-value say?

The comparison reports an unadjusted p-value of 0.477. In general, a p-value is calculated under a specified null hypothesis and statistical model. It measures how often data at least as extreme as the observed data would occur under that model if its assumptions held. It is not the chance that a treatment works, the chance that the null hypothesis is true, or a direct measure of clinical importance.

The registry record does not provide the original statistical analysis plan or a named sponsor analysis for this endpoint. It does not report adjustment for covariates. The p-value should therefore be interpreted as an unadjusted comparison associated with the posted counts, not as evidence that other analyses were performed.

Why do the confidence intervals matter?

A confidence interval gives a range of values compatible with the data and the method used to calculate it. In repeated use of the same method under its assumptions, intervals constructed in this way would contain the true parameter at the stated confidence level at the corresponding frequency. A confidence interval is not a guarantee that the true value lies within the particular interval, nor does it assign probabilities to individual values after the data have been observed.

The risk-difference interval runs from -0.145 to 0.312. It crosses zero, the value representing no absolute difference. The intervals for the risk ratio and odds ratio also include one, their respective no-association values. Their breadth indicates that the data do not estimate the between-arm contrast precisely. The point estimates alone should not be read without these intervals.

What can be inferred from the posted analysis?

The registry lists one primary outcome measure and no secondary outcomes. It lists no analysis entries, although summary comparisons are available for the primary counts. The methods used to classify responses, deal with missing outcomes, and define the analysis set are not reported in the registry record. These are important aspects of interpretation, because a count of responses is informative only in relation to who was assessed and how the endpoint was determined.

In general, random allocation can help make treatment groups comparable at baseline, but it does not guarantee that the analyzed groups remain comparable if post-randomization exclusions or missing outcomes occur. The registry description identifies randomized allocation but does not report details needed to assess these issues. No adjustment, subgroup, sensitivity, or interim analyses are reported. Their absence from the registry record should not be taken as proof that none occurred outside the record.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.083, and its 95% confidence interval extends from -0.145 to 0.312. This interval includes zero and covers a range of contrasts on both sides of no difference. The posted risk ratio of 1.5 has a 95% confidence interval from 0.484 to 4.651; the posted odds ratio of 1.667 has a 95% confidence interval from 0.404 to 6.87. Both ratio intervals include one, the value representing no relative association.

In general, a confidence interval combines the estimated effect with information about its uncertainty under the calculation method. A narrow interval indicates greater precision than a wide interval, while a wide interval leaves more uncertainty about the effect's magnitude. These intervals are broad relative to their point estimates, so the posted data do not pin down a precise comparative response effect. The intervals also allow for effects in opposite directions, making the point estimate's direction uncertain.

The confidence intervals should not be interpreted as ranges that contain every plausible individual outcome, or as a guarantee about the true effect. They concern the comparative effect parameter under the statistical assumptions used. The registry record does not describe those calculation methods in detail, and it does not report an adjusted confidence interval. The unadjusted p-value of 0.477 is consistent with the intervals' inclusion of the no-difference values, but the interval estimates provide more direct information about the range and precision of the effects compatible with the posted counts.

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 table and curve are planning illustrations based on the observed effect, not the trial's original design assumptions. The figures in the table are participants per arm, not total participants or total events. 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 the stated fraction of the observed effect. The original trial's own sample-size justification and planning assumptions are not reported in the registry record.

For planning for 100% of the observed effect, the table gives 372 participants per arm for 80% power and 498 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 637 participants per arm for 80% power and 852 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 1,377 participants per arm for 80% power and 1,842 participants per arm for 90% power.

In general, power is the probability that a study will detect an effect of a specified size under the assumptions used, if that effect is the true one. The 80% and 90% columns describe different target probabilities of detecting the specified effect; the higher target requires more participants under the stated assumptions. The curve illustrates the relation between the planning effect and the sample size. Smaller effects require more participants to detect reliably, as reflected by the increasing figures for smaller fractions of the observed effect.

These figures are not observed power. They are planning estimates based on the observed effect and should not be read as the number enrolled or as a retrospective measure of whether the completed study was successful.

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 = 0.167; treatment proportion p₁ = 0.250; average p̄ = 0.208.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5743 = 1.1257.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5713 = 0.4808.
4. n = (1.1257 + 0.4808)² / (0.0833)² = 371.6, rounded up to 372 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 <- 0.166666666666667                          # control proportion
p1 <- 0.25                          # 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(2368093)
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 = 372 (80% power), 498 (90% power)
 75% of observed effect: n per arm = 637 (80% power), 852 (90% power)
 50% of observed effect: n per arm = 1,377 (80% power), 1,842 (90% power)
power.prop.test: 371.6 
Simulated power at n = 372 per arm: 0.797 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome measure, the good EULAR therapeutic response rate at 6 months, and no secondary outcomes. It does not report whether additional outcomes were measured but not entered in the registry, or whether multiple comparisons were planned in a separate analysis plan. The handling of multiplicity is therefore not reported in the registry record.

In general, multiplicity arises when a study evaluates several outcomes, time points, treatment contrasts, or subgroups. Testing many hypotheses can increase the chance of at least one apparently noteworthy result under a setting where none of the hypotheses represents a true effect. Prespecifying a primary endpoint and a statistical hierarchy can help clarify which comparisons are confirmatory and how others should be interpreted. The registry record identifies a primary endpoint, but it does not provide enough information to assess a wider testing strategy.

The registry lists no analysis entries, and no adjusted analyses are reported. The posted comparison statistics are unadjusted. The statistical analysis plan, any correction for multiple testing, and any prespecified subgroup analyses are not reported in the registry record. It is not possible to determine from the registry information whether the reported comparison was the only analysis conducted.

The record also does not report the number of participants with missing 6-month endpoint data, the reasons for missingness, or how missing outcomes were handled. It does not state whether the endpoint analysis followed an intention-to-treat approach, a per-protocol approach, or another population definition. These details can affect the interpretation of randomized comparisons, especially if missingness or exclusions differ between arms. No imputation, sensitivity analysis, or missing-data assumption is reported.

These omissions do not establish that multiplicity or missing-data methods were absent from the trial's full documentation. They mean that those methods cannot be assessed from the registry record. The posted arm counts and unadjusted estimates should therefore be interpreted without assuming an analysis population or adjustment procedure that is not documented.

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

The posted result describes the number of participants classified as having a good EULAR therapeutic response at 6 months: 6 of 24 in the dextromethorphan arm and 4 of 24 in the placebo arm. The associated risk difference is 0.083. This is a descriptive comparison of the observed groups, accompanied by uncertainty intervals that include no difference and values in either direction.

The data do not establish that the arms had the same response rate. Failure to distinguish a difference in this comparison is not the same as evidence of equivalence. An equivalence conclusion would require an appropriate design and a prespecified range of differences considered sufficiently small; those details are not reported in the registry record. Likewise, the direction of the point estimate is not sufficient to establish a treatment effect.

In general, statistical uncertainty and clinical importance are different questions. Statistical uncertainty concerns how precisely an effect is estimated. Clinical importance requires context about the outcome, relevant thresholds, burdens, and patient priorities. The registry record names the response endpoint but does not report a threshold for clinical importance or other context needed to judge it. The result should not be converted into advice about treatment choices.

The record's information also does not establish how representative the participants were, how consistently the response was measured, or how missing outcomes were handled. The randomized parallel design is relevant to the comparison, but the registry entries are not sufficient to evaluate all features of trial conduct and analysis. No secondary outcomes or analysis entries are listed.

Accordingly, the narrowest defensible reading is that the posted counts show a numerically higher response proportion in the dextromethorphan arm, while the comparison remains imprecise. The registry record does not support a definitive claim about the presence, absence, or clinical importance of a comparative effect.

15. Why This Trial Matters Statistically

This trial is statistically informative as an example of why an observed difference and a reliable estimate are not the same thing. The two arm counts differ, and the point estimates favor a higher response proportion in the dextromethorphan group. Yet the confidence intervals are broad and include the no-difference values. Looking at the counts alone would give an incomplete account of the uncertainty.

The choice to report a binary response endpoint also matters. A binary endpoint reduces each participant's outcome to whether a response criterion was met, rather than showing the full range of disease activity or change. Such endpoints can be useful, but their interpretation depends on the definition and consistent assessment of response. The detailed response criteria and assessment procedures are not reported in the registry record.

The record also illustrates the distinction between a trial's original design and a planning calculation based on an observed estimate. The sample-size illustrations use the observed effect and stated assumptions; they are not evidence about the original planning process, and they are not observed power. The registry's original sample-size rationale is not reported.

Finally, the registry contains limited information about the analysis population, missing outcomes, and analysis plan. Those gaps are statistically consequential because they affect how confidently the posted comparison can be interpreted. Clear reporting of endpoint definitions, participant flow, missing-data handling, and prespecified analyses helps readers distinguish a descriptive result from a well-characterized inferential analysis.

16. 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 posted outcome counts are small: 24 participants are listed in each arm. With this amount of information, the comparative estimates have broad confidence intervals, limiting precision. The interval estimates include the no-difference values and span effects in both directions, so the direction and magnitude of the underlying contrast remain uncertain.

The registry record does not provide the detailed criteria for a good EULAR response, describe who assessed it, or explain assessment procedures. It also does not report baseline disease characteristics, eligibility details, participant flow, treatment adherence, discontinuations, or the number of participants with missing endpoint data. Without these details, it is difficult to judge how the endpoint counts relate to all randomized participants and how the outcome was applied.

No secondary outcomes or analysis entries are listed. The registry record does not report the original sample-size justification, a full statistical analysis plan, adjustment methods, subgroup analyses, or sensitivity analyses. The posted comparisons are unadjusted, and the analysis population is not specified. The registry's lack of these details does not prove they were absent from other trial documentation, but it prevents evaluation from this record.

Safety reporting is also limited. The adverse-event record displays zero values for the at-risk and affected counts in both groups, while deaths are not reported in the registry record. Because the at-risk counts are themselves zero, these entries should not be interpreted as evidence that no adverse events occurred; they do not establish the extent of safety surveillance or the number of participants assessed.

17. Related Tutorials

18. Related Statistical Calculators

19. Sources

• ClinicalTrials.gov: Efficacy Study of Dextromethorphan to Treat Rheumatoid Arthritis — NCT02368093.
• Registry record last updated 2015-03-31; status last verified 2015-03.
• Results first posted 2015-03-31.
• 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.

20. Record Summary

The registry record describes a completed, randomized, quadruple-masked, parallel-group trial of oral dextromethorphan hydrobromide versus placebo as add-on therapy to traditional DMARDs for rheumatoid arthritis. Enrollment is listed as 48. The primary outcome is the number of participants with a good EULAR therapeutic response at 6 months.

The posted counts are 6 of 24 for dextromethorphan and 4 of 24 for placebo. The unadjusted risk difference is 0.083, with a 95% confidence interval from -0.145 to 0.312; the reported unadjusted p-value is 0.477. The estimates are imprecise and do not establish a definitive between-arm difference.

The registry lists no secondary outcomes or analysis entries. The original sample-size rationale, analysis population, missing-data methods, and detailed endpoint criteria are not reported in the registry record.