Soluble Epoxide Hydrolase Inhibition and Insulin Resistance: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Soluble Epoxide Hydrolase Inhibition and Insulin Resistance (NCT03486223), a randomized phase 2 study. The primary outcome is Insulin Sensitivity.

2. Clinical Question

This is a comparison of treatment periods within a randomized crossover trial, rather than a parallel-group trial in which each participant receives only one assigned treatment. The registry describes double masking and randomized allocation. It does not report participant-level characteristics such as age, sex, or baseline metabolic measurements, so the population represented by the results cannot be described more specifically from the registry record.

The registry identifies several related conditions and lists tissue insulin signaling, forearm blood flow, blood pressure, and renal plasma flow among secondary outcomes. Those measures provide context about the study’s broader physiological questions, but the primary endpoint is insulin sensitivity. The record’s results therefore address a specific short-term measurement under the study conditions; they do not by themselves answer broader questions about longer-term outcomes or use in populations beyond those characterized in the record.

3. Trial Design

NCT03486223 is a Phase 2, randomized, double-masked crossover study sponsored by Vanderbilt University Medical Center. The registry lists enrollment of 16 and a completed status. The recorded study start was 2018-05-17, and primary completion was 2021-11-18. The registry describes the study purpose as testing the effects of soluble epoxide hydrolase inhibition with GSK2256294 on tissue sEH activity and insulin sensitivity.

In the crossover design, participants received both GSK2256294 and placebo in one of two sequences. One sequence began with placebo and then switched to GSK2256294; the other began with GSK2256294 and then switched to placebo. Each treatment period was 7 days, with a seven week washout between periods. Randomization assigns the treatment sequence, while double masking means the registry identifies masking at two levels without naming who those masked parties were. That detail is not reported in the registry record.

The primary outcome was assessed on Day 7 of a treatment period. The registry reports mean insulin sensitivity and standard deviation for each treatment, with 15 observations listed for each. These arm-level summaries do not describe how many participants contributed measurements to both periods or explain the difference between the enrollment figure and the outcome counts. The reasons are not reported in the registry record.

A crossover design can make within-participant comparisons possible, because the same participant may contribute observations under both treatments. However, interpretation of such comparisons depends on how the analysis handles paired measurements, treatment sequence, and any period effects. The registry reports a Wilcoxon (Mann-Whitney) analysis for the primary comparison, but further details about handling the crossover structure are not reported in the registry record. The trial’s original sample-size justification and detailed statistical analysis plan are also 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.

Before assignment: 16 individuals were randomized. Of those not randomized, 19 did not meet inclusion criteria and were excluded. 1 participant was randomized but was excluded due to illness prior to receiving any study intervention.

Intervention 1

Reasons for not completing this period:

Washout

Intervention 2

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: 1 participant included here (in GSK-then-placebo arm) was randomized but did not receive intervention or complete a study day

6. Primary Endpoint

The registry lists the primary outcome as Insulin Sensitivity, measured over Day 7.

The primary endpoint is insulin sensitivity, expressed in mg/kg/FFM/min and recorded on Day 7. The registry defines it using the glucose infusion rate (GIR) per fat-free mass (FFM) during high dose insulin infusion in a hyperinsulinemic-euglycemic clamp. In general, a clamp is a controlled experimental method for assessing how much glucose must be infused to maintain the intended glucose conditions during insulin administration. The registry uses the resulting glucose infusion rate, adjusted for fat-free mass, as its measure of insulin sensitivity.

Using fat-free mass in the endpoint expresses glucose infusion relative to the amount of non-fat body mass, rather than as an unadjusted total infusion rate. That can make measurements more comparable across participants whose body composition differs. This is a general explanation of the endpoint’s scaling; the registry does not report why this measure was selected or provide further rationale for the specific procedure.

The endpoint is a continuous measure, reported as a mean with standard deviation for each treatment. Continuous measurements can describe both the direction and size of a difference, while their spread indicates variation among observations. The endpoint is a physiological measurement made during a specified study procedure, not a direct measure of longer-term clinical outcomes. The registry record does not report a minimum clinically important difference or a threshold that would define a meaningful change.

7. Results Posted in the Registry

• GSK2256294: mean 11.60 versus 12.00 on control; difference -0.40 (95% CI -3.27 to 2.47), standardized effect d = -0.10; z-test p = 0.785.

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.

Forearm Blood Flow (FBF)

• 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:
  • GSK2256294: mean 3.10 versus 3.50 on control; difference -0.40 (95% CI -1.60 to 0.80), standardized effect d = -0.26; z-test p = 0.513.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK2256294 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists forearm blood flow, insulin signaling in tissue, blood pressure, and renal plasma flow as secondary outcomes. The detailed numerical secondary summary available in the registry record is for forearm blood flow; the other listed outcomes’ numerical results are not reported in the registry record. As a result, the overall pattern across all secondary endpoints cannot be characterized from the available outcome summaries.

The forearm blood flow summary has a mean of 3.5 ml/min/100ml during placebo and 3.1 ml/min/100ml during GSK2256294. Its recalculated mean difference is -0.4, with a 95% confidence interval from -1.598 to 0.798. The unadjusted recalculated p-value is 0.513. These data do not provide a precise estimate of the treatment-period difference. This secondary result does not resolve the uncertainty around the primary insulin sensitivity result, which is a different measure.

In general, secondary endpoints can offer supporting or exploratory context, but they are often less conclusive when many outcomes are considered. Testing multiple outcomes increases the chance of observing an apparently notable result by chance, especially if no adjustment or prespecified hierarchy is used. The registry does not report whether a multiplicity adjustment was applied or how secondary findings were prioritized. The secondary outcomes should therefore be interpreted cautiously and should not be treated as independent confirmation of the primary result.

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

• Forearm Blood Flow (FBF)
• Insulin Signaling in Tissue
• Blood Pressure
• Renal Plasma Flow (RPF)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary summary compares mean insulin sensitivity during the GSK2256294 and placebo treatment periods. A mean is the arithmetic average of a continuous measurement. In this record, each treatment mean is accompanied by a standard deviation, which describes how spread out the observations are around that mean. The mean difference is stated as GSK2256294 relative to placebo, so a negative estimate indicates a lower posted mean during the GSK2256294 period. The estimate is -0.4 mg/kg/FFM/min.

This difference is a descriptive contrast between treatment periods. It does not by itself establish that treatment caused a difference. A causal interpretation depends on the trial design, conduct, and analysis, including how the crossover structure and possible period effects were handled. Further analysis details are not reported in the registry record.

What is the sponsor’s reported test?

The registry reports a Wilcoxon (Mann-Whitney) test for the primary comparison, with p = 0.71. In general, the Wilcoxon rank-sum approach compares the ordering of observed values between groups rather than directly testing a difference between arithmetic means. Its interpretation depends on the data and analysis context; it should not automatically be treated as a test of a mean difference. The registry does not report additional details about implementation or how the reported test accounted for the crossover design.

The posted-summary recalculation uses the treatment means and standard deviations to produce an unadjusted mean difference, confidence interval, and p-value. Its p-value is 0.785. This calculation is a simple comparison based on the posted summary statistics, not a reconstruction of the participant-level trial analysis. The reported sponsor analysis and the recalculation answer related but not identical statistical questions because they use different methods.

Why does a confidence interval matter?

In general, a confidence interval describes the range of effect estimates compatible with the observed data and the statistical model used to construct the interval. The primary recalculated 95% interval runs from -3.271 to 2.471. Because it includes zero, it does not exclude no difference under that calculation. Its width also indicates that the estimate is imprecise: values on both sides of zero remain compatible with the data. A confidence interval is not a guarantee that the true effect lies within its limits, and it does not state the probability that a particular value is true.

The interval comes from the summary-statistic recalculation, not from the registry’s reported Wilcoxon test. The registry does not report a confidence interval for the sponsor’s test. As a result, the interval should not be presented as an uncertainty interval from the sponsor’s own analysis.

How should the crossover design affect reading?

In general, crossover studies can use within-participant comparisons, which may account for stable differences between participants. Such analyses require information about paired responses or the participant-level data. The registry gives treatment-period means and standard deviations, but does not report a paired standard deviation, within-participant correlation, or participant-level treatment contrasts. The simple recalculation therefore cannot make use of those paired quantities. It is useful as a transparent check on the posted means, but it is not a substitute for a crossover analysis using the underlying data.

The registry’s treatment sequences and washout period are relevant design features, but their presence alone does not show whether carryover or period effects were assessed. Those analyses are not reported in the registry record. It is therefore not possible to determine from the record whether or how such effects influenced the sponsor’s result.

What does the p-value say?

In general, a p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The sponsor-reported p-value of 0.71 and the recalculated p-value of 0.785 are both relatively uninformative about effect magnitude without the estimate and its uncertainty. Neither value is evidence that the treatments are equivalent.

The registry does not report an equivalence or non-inferiority objective, a margin for such a question, or a basis for interpreting the observed difference as clinically negligible. Those elements should not be inferred from a non-significant test.

What is known about the analysis plan?

The record identifies one reported analysis and lists 11 outcome measures, while also listing four secondary outcome domains. It does not report the full analysis plan, the prespecified hierarchy among outcomes, handling of missing observations, or any adjustment for multiple comparisons. These omissions limit assessment of which analyses were planned, how all measured outcomes were handled, and how much emphasis should be placed on individual secondary findings.

11. Confidence Intervals and Precision

The primary recalculated mean difference is -0.4 mg/kg/FFM/min, with a 95% confidence interval from -3.271 to 2.471. The interval spans zero, so the observed summaries do not precisely determine whether insulin sensitivity was higher or lower during the GSK2256294 period. The range also includes differences of varying magnitude. The registry does not provide a threshold for clinical importance, so the interval cannot be classified against a stated meaningful-effect boundary.

In general, a narrower confidence interval indicates greater precision, while a wider interval leaves more uncertainty about the size and direction of an effect. The primary interval is wide in relation to the point estimate. This means the mean difference of -0.4 should not be read as a precise estimate. It also means that failure to exclude zero is not proof that there is no treatment difference.

The interval is a recalculated, unadjusted interval from the posted summary statistics. It is not a confidence interval reported for the sponsor’s Wilcoxon (Mann-Whitney) analysis. Because the trial used a crossover design and the registry does not report paired treatment information, the recalculated interval does not capture all the information that could be used in a participant-level crossover analysis. The registry record does not explain whether the sponsor’s analysis accounted for within-participant pairing or other design features.

Precision should therefore be considered together with the analysis method and the limited information in the registry. The estimate, interval, and sponsor-reported p-value each describe different aspects of the evidence; none provides a stand-alone statement about treatment benefit or lack of benefit.

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 participants per arm, not total event counts. They are illustrations based on the observed effect, not a report of the trial’s original design calculation. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect and model were correct. The 90% power column gives the corresponding planning figure for a 90% chance. These are design calculations, not probabilities that the completed trial’s result is correct. The figures are not observed power.

For insulin sensitivity, planning for 100% of the observed effect gives 1,579 participants per arm for 80% power and 2,114 participants per arm for 90% power. Planning for 75% of the observed effect gives 2,807 participants per arm for 80% power and 3,757 participants per arm for 90% power. Planning for 50% of the observed effect gives 6,315 participants per arm for 80% power and 8,454 participants per arm for 90% power. The pattern illustrates the general principle that smaller effects require more participants to detect, all else being equal.

These figures use the observed effect as their starting point. They are not a recommended study size and do not show what the original investigators intended. They also rely on the stated normal-approximation planning assumptions, rather than reproducing a crossover-specific sample-size calculation from participant-level data.

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 = -0.400; pooled standard deviation σ = 4.011.
2. n = 2 × (1.96 + 0.842)² × 4.011² / -0.400² = 1,578.6, rounded up to 1,579 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 <- -0.4                      # observed difference in means
sigma <- 4.01123422402632                     # 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(3486223)
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 = 1,579 (80% power), 2,114 (90% power)
 75% of observed effect: n per arm = 2,807 (80% power), 3,757 (90% power)
 50% of observed effect: n per arm = 6,315 (80% power), 8,454 (90% power)
power.t.test: 1579.6 
Simulated power at n = 1,579 per arm: 0.800 (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 registry reports that the sponsor’s primary comparison used a Wilcoxon (Mann-Whitney) method and yielded p = 0.71. The recalculation from the posted means and standard deviations gives a mean difference of -0.4 and an unadjusted p-value of 0.785, with a 95% confidence interval from -3.271 to 2.471. The recalculated result is a summary-statistic comparison of means; it is not a reproduction of the sponsor’s rank-based test.

Differences between the p-values are expected when analyses use different methods and statistics. The rank-based test evaluates the ordering of observations, while the recalculation estimates a mean difference from the arm-level summaries. The registry does not provide individual observations or sufficient details to reproduce the sponsor’s analysis exactly, or to explain the numerical difference between the results.

The sponsor’s result should be read as the analysis reported in the registry. The recalculation offers a separate, transparent description of the posted mean summaries and their uncertainty. Neither should be treated as a substitute for the other, and neither p-value alone communicates precision or clinical importance. The registry does not report an interval estimate alongside the sponsor’s test.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 11 outcome measures and four secondary outcome domains. It reports one analysis for the primary comparison, but does not provide a complete analysis plan explaining how the outcomes were prioritized or how many comparisons were planned. It also does not report whether statistical adjustment for multiple comparisons was performed. Without that information, the degree to which the reported findings account for the number of outcomes examined is not known.

In general, multiplicity arises when several statistical tests are conducted. The more comparisons made, the greater the chance that at least one result may appear notable even when there is no underlying effect. Adjustment methods or a prespecified hierarchy can address this concern, but the registry record does not identify such methods for this study. Individual secondary results should consequently be treated as exploratory unless further analysis documentation establishes otherwise.

The record does not report how missing outcome measurements were handled, whether all randomized participants were included in each analysis, or which analysis population was used. Although the primary outcome summaries list 15 observations under each treatment and the enrollment is 16, the reason for this difference is not reported in the registry record. The available summaries do not establish whether the same participants contributed under both treatments, whether any measurements were missing, or how missingness was addressed.

For a crossover study, paired observations, treatment sequence, and period can be relevant to analysis. The registry provides the treatment sequences and washout description, but does not report analyses of period effects, carryover, or sequence effects. These details are important when judging whether the statistical analysis reflects the design. Their absence from the registry record limits independent assessment; it does not establish that these issues were or were not addressed elsewhere.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events and zero deaths in each treatment group. It reports two other adverse events under placebo and two under GSK2256294. These are the recorded counts for the treatment groups as listed; they are not evidence by themselves that the treatments have the same safety profile.

The groups each list 15 participants at risk for serious adverse events and for other adverse events. Because the study is a crossover trial, participants could contribute to more than one treatment period. The registry’s group-level figures do not state whether the same individuals experienced events in both periods, nor do they provide event terms for the non-serious adverse events. The serious-event terms list is empty.

These safety counts describe what the registry reports during the study, but the record does not provide event timing, severity details beyond the serious-event classification, duration, or an analysis comparing risks. With a small trial and limited event information, the counts offer a descriptive record rather than a precise estimate of uncommon harms. They should not be interpreted as proof of safety or of equivalence between treatments.

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

The registry’s primary outcome summaries show mean insulin sensitivity of 12.0 mg/kg/FFM/min during placebo and 11.6 mg/kg/FFM/min during GSK2256294. The unadjusted recalculation estimates a mean difference of -0.4, with a 95% confidence interval from -3.271 to 2.471. The interval includes zero and is broad, so the posted summaries do not precisely establish either the direction or size of a treatment-period difference.

The sponsor’s reported Wilcoxon (Mann-Whitney) analysis gives p = 0.71. That test and the mean-based recalculation are different analyses. Both should be understood in the context of the registry’s limited methodological detail, especially the absence of reported participant-level paired information for the crossover comparison. The results do not establish equivalence, because the registry does not report an equivalence objective or margin.

The finding is specific to the short treatment periods, the Day 7 clamp measurement, and the participants represented in this trial. The registry does not provide enough participant characteristics to describe the study population in detail. It also does not report evidence about longer-term outcomes. The data cannot establish what the treatment might do outside the measured setting or in populations not characterized by the record.

The study’s listed secondary outcomes broaden the physiological questions, but numerical results for all listed outcomes are not reported in the registry record. The available secondary summary does not change the uncertainty around the primary endpoint. Likewise, the reported adverse-event counts are descriptive and do not establish that the treatments have equivalent safety profiles.

In general, a non-significant result is not proof of no effect. It indicates that the analysis did not provide strong evidence against its null model at the stated level of analysis. The confidence interval is useful because it displays the range of values compatible with the recalculation, including effects in both directions. Without a clinical-importance threshold, it is not possible to determine from the registry whether any particular value in that range would matter clinically. These are statistical interpretations of the posted data, not medical advice.

18. Why This Trial Matters Statistically

This trial illustrates how a registry result should be read through both its design and its analysis. The crossover structure means participants received both treatments in different sequences, with a washout between periods. Yet the posted numerical summaries are treatment-level means and standard deviations, and the registry does not report paired differences or the details needed to reconstruct a participant-level crossover analysis. The distinction matters because a summary-statistic recalculation cannot use all the information that may be available in paired data.

The record also makes clear why a p-value is not enough to characterize a result. The sponsor-reported rank-based p-value and the recalculated mean-based estimate answer related but different questions. The mean difference and confidence interval convey direction and uncertainty, while the p-values alone do not describe the size of a possible effect. Neither analysis establishes equivalence.

The sample-size illustrations highlight another important statistical point: planning figures depend on the effect a future study aims to detect. When the target effect is a smaller fraction of the observed effect, the illustrative participant requirement rises. Because these calculations are based on the observed effect and specified planning assumptions, they should not be confused with the trial’s original design rationale or with an assessment of the completed study’s power.

Finally, the registry lists multiple outcomes but does not report a multiplicity strategy or complete numerical summaries for every listed secondary outcome. That limits how confidently individual secondary findings can be treated as confirmatory. Taken together, the record demonstrates the value of distinguishing descriptive summaries, reported tests, recalculated estimates, and planning illustrations rather than treating them as interchangeable evidence.

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 registry does not report the participant characteristics needed to assess how closely the enrolled population reflects any broader clinical population. It lists relevant conditions, but gives no detailed demographic profile or eligibility criteria in the information available. Generalizability therefore cannot be assessed in detail from the record.

Although treatment sequences and a washout period are described, the registry does not report participant-level paired results, treatment-by-period details, or analyses of possible period, sequence, or carryover effects. Those omissions limit interpretation of the crossover comparison. The treatment-period means and standard deviations alone do not show how measurements were paired within participants.

The primary results list 15 observations in each treatment group, while enrollment is 16. The record does not explain the difference or report how missing measurements were handled. It also does not identify the analysis population or clarify whether the outcome summaries include all randomized participants. The reported sponsor test and the summary-statistic recalculation use different methods, and the registry does not provide enough detail to reproduce the sponsor analysis.

The record does not report a clinical-importance threshold, an equivalence margin, or the rationale for selecting the endpoint. It also does not report the original sample-size assumptions, a full statistical analysis plan, or whether multiplicity adjustment was performed. Although several secondary domains are listed, numerical results for all of them are not reported in the registry record. Safety reporting is limited to event counts without detail on non-serious event terms or timing. These limitations constrain interpretation but do not, by themselves, show that the study was conducted improperly.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Soluble Epoxide Hydrolase Inhibition and Insulin Resistance — NCT03486223.
• Registry record last updated 2023-03-23; status last verified 2023-03.
• Results first posted 2023-03-23.
• 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

NCT03486223 is a completed Phase 2 randomized, double-masked crossover study sponsored by Vanderbilt University Medical Center. Enrollment was 16. Participants received 7-day periods of GSK2256294 and placebo in randomized sequences, separated by a seven week washout.

The primary endpoint was Day 7 insulin sensitivity measured by hyperinsulinemic-euglycemic clamp as glucose infusion rate per fat-free mass. The posted means were 12.0 with placebo and 11.6 with GSK2256294. The summary-statistic recalculation estimated a mean difference of -0.4, with a 95% confidence interval from -3.271 to 2.471 and an unadjusted p-value of 0.785. The sponsor-reported Wilcoxon (Mann-Whitney) analysis gave p = 0.71.

The primary interval is compatible with differences in either direction and is not precise. The registry does not report enough paired-data or analysis-plan detail to independently reproduce a crossover analysis or assess all listed secondary outcomes. Safety counts were zero serious adverse events and zero deaths in each treatment group, with two other adverse events reported for each.