Exposure Study Comparing 3 Routes of Methotrexate (MTX) Administration: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Exposure Study Comparing 3 Routes of Methotrexate (MTX) Administration (NCT01737944), a randomized phase 1, phase 2 study. The primary outcome is Bioequivalence Based Upon Dose-Normalized AUC[0-Inf] for MTX.

2. Clinical Question

3. Trial Design

This was a randomized, open-label, crossover study listed in phase 1 and phase 2. The registry reports enrollment of 38 and a completed status. The study began in 2011-01, with primary completion in 2011-05. Its official title describes an exposure, safety, and local-tolerance comparison of the Vibex-MTX device, subcutaneous administration, and intramuscular administration in adults with rheumatoid arthritis.

The treatment arms identify Arm A as subcutaneous MTX using the Vibex device, Arm B as subcutaneous MTX without the device, and Arm C as intramuscular MTX. Dose groups are listed for 10mg, 15mg, 20mg, and 25mg. The primary-outcome summaries report 36 participants in each arm. Safety summaries are organized by dose group and report 9 at risk in each group for the listed safety outcomes.

In general, a crossover study compares treatments across periods in the same participants, which can reduce the influence of stable differences between individuals. The registry record does not report the treatment sequence, number of periods, washout arrangements, or whether all participants completed every treatment. It also does not describe a masking procedure; masking is listed as none. The registry does not report the rationale for the planned enrollment, the original design assumptions, or details of any interim analyses.

The registry’s primary-outcome population is narrower than the randomized population definition: participants had to receive at least one dose and have at least one valid post-dose plasma concentration measurement. The record does not report the reasons for any difference between enrollment and the numbers contributing to each treatment-arm summary. Therefore, the outcome summaries should be read using their stated arm sizes rather than treating enrollment as the analysis denominator.

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.

Before assignment: The order of Methotrexate (MTX) treatment arms (A-SC injection with Vibex-MTX device, B-SC injection without device and C-IM Injection) were randomly assigned and dosing was separated by interval of atleast 7 days to allow for washout before the next treatment was administered.

Overall Study

Analysis population for the primary outcome, as defined in the registry: The Population was defined as all randomized subjects who received at least 1 dose of study drug and who had at least 1 valid post-dose plasma concentration value.

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: 38 subjects were randomized to a treatment sequence. Two subjects discontinued prior to receiving the first study drug dose. Safety Population = 36 subjects who received study drug and completed all study visits. All 36 subjects were included in Pharmacokinetic Population. No discontinuations after first study drug dose.

6. Primary Endpoint

The registry lists the primary outcome as Bioequivalence Based Upon Dose-Normalized AUC[0-Inf] for MTX, measured over 24 Hour period.

The primary endpoint is dose-normalized area under the plasma concentration-time curve from time zero to infinity, written in the registry as AUC[0-Inf]/Dose. Its unit is ng*hr/mL/mg, and its stated timeframe is a 24 Hour period. The registry describes the endpoint as the mean of a continuous measure, with standard deviation as its dispersion statistic.

In general, area under the curve represents cumulative drug exposure across the measured concentration-time profile. Extending the curve to infinity estimates exposure beyond the final observed time point; the precise estimation procedure is not reported in the registry record. Dose-normalization expresses exposure relative to the administered dose, which is useful when comparing exposure across dose levels. That general rationale does not establish how the registry handled different doses in its calculations.

The endpoint is used to compare systemic exposure between administration approaches. The registry labels the primary objective as bioequivalence based on this measure. A bioequivalence judgment ordinarily depends on prespecified criteria for an acceptable range of ratios, but those criteria and the analysis method are not reported in the registry record. The posted arm summaries and the reported test-to-reference ratios can describe the observed exposure results, but they do not by themselves reveal the criterion used by the sponsor.

7. Results Posted in the Registry

• Treatment Arm B: mean 122.63 versus 118.14 on control; difference 4.49 (95% CI -14.67 to 23.65), standardized effect d = 0.11; z-test p = 0.646.
• Treatment Arm C: mean 116.71 versus 118.14 on control; difference -1.43 (95% CI -20.76 to 17.90), standardized effect d = -0.03; z-test p = 0.885.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry identifies the primary outcome as a continuous measure summarized by its mean and standard deviation. General explanation: the mean describes the central value of the observed measurements, while the standard deviation describes how spread out individual measurements are around that mean. A standard deviation is not the same as a confidence interval: it describes variation among measurements, whereas a confidence interval expresses uncertainty around an estimated quantity.

What do the recalculated comparisons represent?

The posted recalculations compare each of Arms B and C with Arm A using differences between the reported means. They are explicitly unadjusted recalculations from the posted summary statistics. The Arm B comparison is a mean difference of 4.49, and the Arm C comparison is a mean difference of -1.43. The confidence intervals and unadjusted p-values accompany those estimated differences. They are not the sponsor’s reported test-to-reference ratio analyses.

General explanation: a mean difference keeps the comparison in the original measurement units, while a ratio expresses one treatment’s measure relative to another. The difference is useful for understanding the size and direction of an absolute change. A ratio is often used in exposure comparisons because it expresses relative exposure. The registry does not state the method used to calculate the sponsor’s ratios, and the posted summaries do not provide enough information to reconstruct a crossover-adjusted analysis.

Why does the crossover design matter?

In general, crossover analyses can use the fact that each participant receives multiple treatments, comparing observations within the same participant. Such an approach can account for stable participant-level differences and may differ from a comparison that treats arm summaries as independent. The registry identifies a crossover model, but does not report the treatment sequence, period structure, washout, within-participant correlation, or the specific statistical model. The recalculated comparisons are unadjusted comparisons of posted summary statistics; they should not be mistaken for a reconstruction of the trial’s full crossover analysis.

The posted mean differences have confidence intervals from -14.67 to 23.65 for Arm B versus Arm A and from -20.76 to 17.9 for Arm C versus Arm A. Each interval includes zero. The accompanying unadjusted p-values are 0.646 and 0.885, respectively. A p-value describes how unusual data at least as inconsistent with a specified null model would be if that model held, subject to the method’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure the probability that the observed result will replicate.

How do the sponsor results differ in form?

The registry reports a test-to-reference ratio with a 90% confidence interval for each comparison: 96.24 (92.33 to 100.31) for Arm B versus Arm A, and 101.28 (97.17 to 105.56) for Arm C versus Arm A. The registry classifies these as non-inferiority or equivalence analyses, but the method and the acceptable equivalence bounds are not reported in the registry record. Those missing details matter because an interval’s relation to a prespecified margin, rather than simply its relation to a central value, is relevant to such a conclusion.

The registry lists three outcome measures and six analyses. It does not report whether or how the analyses accounted for multiplicity, how missing measurements were handled, or whether sensitivity analyses were conducted. For the primary outcome, the stated population includes randomized participants who received at least one dose and had at least one valid post-dose concentration measurement. That definition clarifies who could contribute, but does not describe imputation or other missing-data procedures. The original statistical plan and assumptions are not reported in the registry record.

10. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals generally indicate less uncertainty about the estimated quantity, while wider intervals leave more plausible values compatible with the data. General explanation: a confidence interval is constructed using a statistical method and its assumptions; it is not a range that is guaranteed to contain the true value, nor does it mean that each value inside it is equally likely.

For the unadjusted Arm B versus Arm A mean difference, the 95% confidence interval runs from -14.67 to 23.65 around the estimate of 4.49. For Arm C versus Arm A, it runs from -20.76 to 17.9 around the estimate of -1.43. Both intervals include zero and span values in both directions. Thus, the recalculated summaries do not pin down the direction of a difference with high precision. The registry reports standard deviations of 42.3, 40.65, and 41.39 for Arms A, B, and C, respectively, describing variability in the measured values.

The sponsor’s reported ratio intervals use a different scale and confidence level. The 90% interval is 92.33 to 100.31 for Arm B versus Arm A and 97.17 to 105.56 for Arm C versus Arm A. These intervals should be considered with the sponsor’s analysis method and prespecified decision criteria, neither of which is reported in the registry record. The intervals alone do not establish whether the study met a bioequivalence criterion.

Because the recalculated intervals are based on posted summaries and are unadjusted, they do not capture every feature of a crossover analysis. Their precision should not be equated with that of the sponsor’s analysis.

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 planning figures are illustrations based on the observed effects, not the original trial’s design assumptions. They report participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The registry record does not report the original design’s sample-size assumptions.

For the Arm B versus Arm A comparison, planning for 100% of the observed effect gives 1,340 participants per arm for 80% power and 1,794 participants per arm for 90% power. Planning for 75% of the observed effect gives 2,383 participants per arm for 80% power and 3,189 participants per arm for 90% power. Planning for 50% of the observed effect gives 5,360 participants per arm for 80% power and 7,175 participants per arm for 90% power.

For the Arm C versus Arm A comparison, planning for 100% of the observed effect gives 13,445 participants per arm for 80% power and 17,999 participants per arm for 90% power. Planning for 75% of the observed effect gives 23,902 participants per arm for 80% power and 31,998 participants per arm for 90% power. Planning for 50% of the observed effect gives 53,779 participants per arm for 80% power and 71,994 participants per arm for 90% power.

In plain terms, the 80% and 90% columns describe the planned probability of detecting the specified effect under the stated assumptions if that effect were real. The 90% target requires more participants per arm than the 80% target. A smaller target effect also requires more participants per arm. These figures are not observed power; they are planning illustrations, and they do not establish the adequacy of the trial’s original design.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 4.490; pooled standard deviation σ = 41.482.
2. n = 2 × (1.96 + 0.842)² × 41.482² / 4.490² = 1,339.9, rounded up to 1,340 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 <- 4.48999999999999                      # observed difference in means
sigma <- 41.4822245305143                     # 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(1737944)
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 = 1,340 (80% power), 1,794 (90% power)
 75% of observed effect: n per arm = 2,383 (80% power), 3,189 (90% power)
 50% of observed effect: n per arm = 5,360 (80% power), 7,175 (90% power)
power.t.test: 1340.9 
Simulated power at n = 1,340 per arm: 0.801 (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.

13. Analyses Reported by the Sponsor

The registry’s own analyses report test-to-reference ratios and 90% confidence intervals: 96.24 (92.33 to 100.31) for Treatment Arm B compared with Arm A, and 101.28 (97.17 to 105.56) for Treatment Arm C compared with Arm A. The registry categorizes these as non-inferiority or equivalence analyses. The analysis method, ratio scale details, and decision margins are not reported in the registry record.

The unadjusted recalculations use the posted means and standard deviations to estimate mean differences, with 95% confidence intervals and unadjusted p-values. These are not the same estimand or analysis as the sponsor’s test-to-reference ratios. The record does not identify the statistical procedure behind the sponsor results, so the recalculations cannot verify or replace it. The discrepancy indicator is false; the recalculations therefore do not flag a conflict with the sponsor’s reported values. For interpretation of the sponsor’s stated analysis, the registry’s own results remain the relevant reported analysis, while its missing methods and equivalence criteria limit independent assessment.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists three outcome measures and six analyses, but does not report whether the analyses were treated as a single family of hypotheses or whether any multiplicity adjustment was used. When several outcomes or comparisons are examined, the chance of at least one apparently unusual result can increase. General explanation: multiplicity procedures manage that issue by adjusting interpretation or testing across related analyses. Without a reported plan, it is not possible to determine how multiple comparisons were handled.

The registry reports the primary-outcome population as randomized participants who received at least one dose and had at least one valid post-dose plasma concentration value. It does not report a missing-data strategy, imputation method, or sensitivity analysis for participants without valid measurements. The endpoint summaries show 36 participants in each treatment arm, while enrollment is 38; reasons for the difference are not reported in the registry record. No total across arms should be inferred from the treatment-arm summaries, particularly for a crossover study.

The registry identifies a crossover model but does not report whether the sponsor’s analysis included period, sequence, participant, or carryover effects, or how within-participant dependence was modeled. These are relevant features of crossover data, but their treatment cannot be inferred from the design label alone. The recalculated mean comparisons are unadjusted and are not a substitute for the original model.

The sponsor’s reported analyses are categorized as non-inferiority or equivalence, but the registry does not state the statistical method, margins, or decision rule. It also does not report the original statistical analysis plan or interim analyses. These omissions limit evaluation of whether the reported analyses followed prespecified procedures and how robust the conclusions are to alternative assumptions.

15. 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 2.8% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event summaries are organized by MTX dose group. For each of the 10mg, 15mg, 20mg, and 25mg groups, 9 participants are listed as at risk, and 0 are listed as affected by serious adverse events. These are group-specific counts as recorded; the registry does not provide a detailed serious-event term list, and no deaths count is reported in the registry record.

The registry also reports other adverse events in the dose-group summaries: 1 affected participant in the 10mg group, 0 in the 15mg group, 2 in the 20mg group, and 1 in the 25mg group, each with 9 at risk. These other-event counts should not be confused with serious adverse events. The record does not give enough detail to identify event types, timing, severity beyond the serious-versus-other categorization, or their relation to a specific administration route.

Small group counts can provide limited information about uncommon events. The registry’s safety summaries should therefore be read as descriptive counts, not as a precise comparison of risk between routes or as evidence that serious events could not occur.

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

The posted results describe dose-normalized MTX exposure across three administration approaches in a randomized crossover study of adults with rheumatoid arthritis. The treatment-arm means are 118.1 for Vibex-assisted subcutaneous administration, 122.6 for subcutaneous administration without the device, and 116.7 for intramuscular administration, in ng*hr/mL/mg. The unadjusted differences are modest relative to the uncertainty expressed by their confidence intervals, which include zero.

The sponsor’s reported test-to-reference ratios are near 100, with 90% confidence intervals of 92.33 to 100.31 and 97.17 to 105.56. The registry labels these as non-inferiority or equivalence analyses. However, without the method and prespecified margins, the record does not allow an independent determination of whether a formal bioequivalence criterion was met. Similar-looking point estimates alone do not establish equivalence.

The endpoint is pharmacokinetic exposure, not a direct measure of rheumatoid arthritis symptoms, disease activity, function, or long-term outcomes. The registry does not post secondary outcome results. Therefore, the exposure findings should not be read as evidence about comparative clinical benefit, and they do not support advice about which route to use.

The safety counts report no participants affected by serious adverse events in any of the listed dose groups. These summaries are limited in scope and size, and the registry does not report detailed event terms or route-specific safety comparisons. Absence of a reported serious event in these counts does not establish absence of risk.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a crossover design with a pharmacokinetic endpoint and a comparison framed as bioequivalence. Crossover designs can make within-participant comparisons informative when the sequence and period effects are adequately addressed. Yet the registry’s design label alone does not reveal how those features entered the analysis. The sponsor’s model and other crossover details are not reported in the registry record.

The example also illustrates why different summaries answer different questions. Means and unadjusted mean differences show absolute exposure on the endpoint’s scale. Test-to-reference ratios describe relative exposure and are the sponsor’s reported form of analysis. Their confidence intervals have different levels from the recalculated mean-difference intervals, and their interpretation depends on the prespecified criterion for equivalence. Since the registry does not state that criterion, apparent proximity to a ratio of 100 cannot establish the formal result.

Precision is central: the recalculated confidence intervals are wide enough to include differences in either direction. The planning illustrations likewise show how the required number of participants per arm increases when the target effect is made smaller. These illustrations are not the study’s original sample-size plan and do not substitute for the sponsor’s analysis.

Finally, the registry record makes clear the difference between pharmacokinetic exposure and clinical outcomes. Statistical interpretation must remain tied to the measured endpoint, the reported population, and the limits of the available analysis details.

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 trial-specific details needed to assess the reported comparisons are not reported in the registry record. These include the crossover treatment sequence, period structure, washout arrangements, handling of possible carryover, and the method used for the sponsor’s test-to-reference ratios. Without those details, the recalculated unadjusted differences cannot be treated as a reproduction of the sponsor’s crossover analysis.

The registry does not report the equivalence margins or decision rule, so the reported ratios and 90% confidence intervals cannot be independently judged against a formal criterion. It also does not report how missing concentration measurements were handled, why the primary-outcome summaries include 36 participants per arm when enrollment was 38, or whether the analyses used any adjustment for multiple comparisons.

The results concern dose-normalized exposure over the stated 24 Hour period and do not provide evidence about clinical outcomes. The safety record offers limited counts by dose group, without detailed event terms or route-specific breakdowns. The sample-size illustrations are based on observed effects rather than the original design; the original sample-size justification is not reported in the registry record. These limitations constrain how much can be concluded from the posted results, even though the endpoint summaries and sponsor analyses are reported.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Exposure Study Comparing 3 Routes of Methotrexate (MTX) Administration — NCT01737944.
• Registry record last updated 2014-02-25; status last verified 2014-01.
• Results first posted 2014-02-25.
• 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

NCT01737944 is a completed randomized, open-label crossover study of MTX administration by Vibex-assisted subcutaneous injection, subcutaneous injection without the device, and intramuscular injection in adults with rheumatoid arthritis. The registry lists phase 1 and phase 2, enrollment of 38, a start in 2011-01, and primary completion in 2011-05.

The primary endpoint is dose-normalized AUC[0-Inf] over a 24 Hour period, measured in ng*hr/mL/mg. Posted treatment-arm summaries include 36 participants per arm. The registry reports test-to-reference ratios and 90% confidence intervals for both comparisons, alongside unadjusted recalculations based on the posted summaries. The crossover analysis method, equivalence margins, missing-data procedures, multiplicity handling, and original design assumptions are not reported in the registry record.