Sotagliflozin Safety and Tolerability Among Renal Transplant Recipients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Sotagliflozin Safety and Tolerability Among Renal Transplant Recipients (NCT05405556), a randomized phase 2 study. The primary outcome is Reversibility of eGFR Changes.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 2 trial with no masking. The registry describes the intervention as eGFR reporting. Participants were assigned to one of two communication strategies: reporting study eGFR values only when they were more than 25% below baseline, or reporting all study eGFR measurements to the participant and treating physician. The trial summary describes open-label sotagliflozin treatment, with the primary outcome assessed after treatment stopped.

The planned observation period for the primary endpoint was 16 weeks total: 12 weeks of drug treatment followed by four weeks off treatment. The primary outcome concerned return of eGFR to within plus or minus 10% of baseline by the end of that off-treatment period. The registry lists the primary completion date as 2024-05-10 and the study status as completed. Its start date is 2022-10-17.

The registry lists enrollment as 40, while the brief summary describes the trial as involving N=50. The results are presented for 19 participants in one randomized group and 21 in the other. The registry record does not explain the difference between its enrollment entry and summary description, or provide a flow accounting for participants from enrollment to analysis. The listed sponsor is Martina McGrath, MD.

The study is not a masked drug-versus-control trial. Its randomized comparison is between reporting policies during sotagliflozin treatment. This distinction matters when interpreting the result: the primary contrast concerns whether participants and clinicians were informed about study eGFR measurements according to one policy or the other. The registry record does not report the original sample-size justification or the detailed statistical plan.

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 Reversibility of eGFR Changes, measured over 16 weeks total.

The primary endpoint is the number of participants who returned to a specified range around their baseline eGFR after stopping treatment. The registry defines this as eGFR within plus or minus 10% of baseline at the end of the four-week off-treatment period. It is therefore a binary participant-level outcome: each participant either met the return-to-baseline criterion by the stated time or did not.

This endpoint was selected to assess whether the acute eGFR changes expected during sotagliflozin treatment were reversible after treatment ended. Measuring the outcome after an off-treatment period makes the endpoint about the observed eGFR trajectory across treatment and follow-up, rather than only the value during drug exposure. The trial summary also identifies completion under different eGFR reporting strategies and safety and tolerability as aims.

The posted primary counts are 13 of 19 in the restricted-reporting group and 16 of 21 in the all-results-reporting group. Those counts describe how many participants met the endpoint in each group; they do not by themselves show why any participant did or did not return to the defined range. The registry record does not report additional endpoint detail about handling measurements that were unavailable at the assessment time.

7. Results Posted in the Registry

• Patients and Providers Aware of All Study eGFR Values: 76.2% (16/21) versus 68.4% (13/19) on control; risk difference 7.8 percentage points (95% CI -20.0 to 35.5), risk ratio 1.11 (0.76–1.64); unadjusted two-proportion z-test p = 0.583.

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.

Proportion of Patients Successfully Completing the Full Treatment Protocol, According to Randomized Groups

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Patients and Providers Aware of All Study eGFR Values: 85.7% (18/21) versus 94.7% (18/19) on control; risk difference -9.0 percentage points (95% CI -27.0 to 9.0), risk ratio 0.90 (0.74–1.11); unadjusted two-proportion z-test p = 0.342.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Patients and Providers Aware of All Study eGFR Values and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoint concerns completing the full treatment protocol according to randomized group. Its overall pattern differs from the primary endpoint in an important way: the group with the higher primary endpoint count does not also have the higher completion proportion. This means completion does not provide a simple supporting pattern for the primary result.

The secondary endpoint addresses a related but distinct question. Returning to the baseline eGFR range is a physiological outcome at the end of the off-treatment period, while completing the protocol captures whether participants finished the treatment protocol. A participant can contribute differently to these two endpoints, so they should not be treated as alternate measurements of the same outcome.

Secondary results generally carry less weight than the primary result when they are not supported by a prespecified testing hierarchy or a clear multiplicity strategy. Examining multiple outcomes increases the opportunity for chance findings, and unadjusted p-values do not account for that. The registry record lists 17 outcome measures, but the handling of multiple comparisons is not reported in the registry record. The posted secondary comparison is unadjusted, and no secondary reported analyses are listed.

These considerations do not make the secondary outcome irrelevant. It can add descriptive context about study completion. However, it should not be used alone to confirm or overturn the primary endpoint, especially given the uncertainty in both comparisons and the absence of reported analysis details. The secondary result is best interpreted as a separate, exploratory-looking piece of evidence unless the registry record's prespecified analysis plan establishes otherwise; such a plan is not reported in the registry record.

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

• Proportion of Patients Successfully Completing the Full Treatment Protocol, According to Randomized Groups

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, such as whether a participant returned to the defined eGFR range, the basic comparison is the proportion meeting the endpoint in each randomized group. A risk difference expresses the contrast as the proportion in one group minus the proportion in the other. A positive estimate in this comparison means the observed proportion was higher in the group assigned to report all study eGFR values. The estimate is an observed contrast, not proof that reporting policy caused the difference.

What does the confidence interval add?

A confidence interval describes the range of effect estimates compatible with the data under the method used to calculate it. It gives more information than a point estimate alone because it indicates how uncertain that estimate is. For the primary comparison, the interval crosses the no-difference value and reaches into both directions. This means the data are compatible with the all-results-reporting group having a higher endpoint proportion, with little or no difference, or with a lower proportion. The interval does not identify which of those possibilities is true.

The unadjusted p-value is 0.583 for the primary comparison. A p-value measures how unusual data at least as incompatible with the no-difference hypothesis would be under that hypothesis and the statistical model. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. An unadjusted p-value also does not account for the fact that multiple outcomes or comparisons may have been examined. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the outcomes.

Why use a risk difference?

The risk difference is an absolute-scale measure: it describes how far apart the two observed proportions are, rather than expressing one proportion relative to the other. Absolute contrasts can be easier to relate to the event frequency in the trial groups. Relative measures, such as a risk ratio or odds ratio, answer different questions and can appear more or less pronounced depending on the baseline event frequency. For this reason, the measures should not be treated as interchangeable. The posted analysis identifies the risk difference as its comparison metric.

For any binary outcome, counts and denominators are important context. The primary counts are 13 of 19 and 16 of 21. With modest group sizes, a small change in the outcome count can noticeably affect the estimated proportions and the contrast between groups. Uncertainty is therefore important even when the point estimate has a clear direction. The posted interval is a reminder that the observed group difference is not estimated with enough precision to rule out effects in either direction.

What does randomization contribute?

Random allocation is intended to make the assigned groups comparable, on average, with respect to factors that could influence the outcome. In a small trial, randomization does not guarantee that all prognostic characteristics will be balanced. No baseline characteristics are included in the registry entries for this analysis, so the balance of specific participant features is not reported in the registry record. The absence of masking is also relevant: participants and providers knew the assigned eGFR reporting strategy. The record does not say whether outcome assessment was masked.

The randomized comparison estimates the contrast between the reporting strategies as implemented in the trial setting. It does not isolate every possible behavioral or clinical response to seeing eGFR values. Reporting all results could affect decisions or follow-up, while a restricted reporting rule could affect what participants and clinicians know. The posted endpoint alone does not describe those pathways.

What analyses are available?

The registry lists 17 outcome measures and one posted secondary outcome, but reports zero analyses and no reported analyses for the secondary outcome. The comparison results displayed for the primary and posted secondary endpoint are unadjusted. The registry record does not report the analysis population, missing-data method, covariate adjustment, or whether the results follow an intention-to-treat principle. These details matter because exclusions, unavailable eGFR measurements, and choices about which participants to analyze can affect a binary endpoint estimate.

The term “unadjusted” here means the comparison is not presented as adjusted for other participant characteristics or for multiple testing. It does not imply that the posted result is necessarily incorrect. It indicates that interpretation should remain close to the reported group counts and uncertainty, without assuming that a model accounts for other sources of variation. The record does not report a more detailed model or a plan for sensitivity analyses.

11. Confidence Intervals and Precision

The primary risk-difference estimate is positive for the group assigned to report all study eGFR values, but the confidence interval spans the no-difference value and extends to both sides. This is the central precision point: the result does not pin down the direction of the underlying difference. The p-value of 0.583 is consistent with that uncertainty, but it should not replace examination of the interval and observed counts.

The group counts are 13 of 19 and 16 of 21. With this amount of information, the estimated proportions can be sensitive to the outcomes of a small number of participants. The interval is consequently broad enough that materially different interpretations remain compatible with the data. It does not support a narrow claim about the size of a difference between reporting strategies.

The secondary completion comparison is also imprecise. Its interval crosses the no-difference value, and the unadjusted p-value is 0.342. As with the primary endpoint, the interval should be read as a range of estimates compatible with the observed data under the analysis method, not as a probability distribution over the true effect.

Confidence intervals do not address every limitation. They do not correct for missing outcomes, multiplicity, selection into the analysis, or measurement issues unless those are explicitly incorporated in the method. The registry record does not report how such issues were handled. The intervals therefore describe statistical uncertainty under the posted comparison, while other uncertainties remain unresolved.

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 expressed as participants per arm, not total participants or total events. They are illustrations based on the observed effect, not the original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The figures show planning for 100%, 75%, and 50% of the observed effect.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the assumed effect under those planning assumptions, if that effect is real and the assumptions hold. The 90% power column gives the corresponding planning count for a 90% chance. These are design targets, not guarantees about the results of a future trial. The original trial's own sample-size assumptions and justification are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 520 participants per arm for 80% power and 696 participants per arm for 90% power. Planning for 75% gives 945 participants per arm for 80% power and 1,264 participants per arm for 90% power. Planning for 50% gives 2,168 participants per arm for 80% power and 2,902 participants per arm for 90% power. The secondary endpoint has its own planning illustrations based on its observed effect.

Smaller assumed effects require more participants because they are harder to distinguish from random variation. These calculations are not observed power; they are sample-size planning illustrations using the stated assumptions and the observed effect as a starting point. The planning curve represents the same relationship: as the assumed effect becomes smaller, the required participants per arm increase.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.684; treatment proportion p₁ = 0.762; average p̄ = 0.723.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6328 = 1.2403.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6305 = 0.5306.
4. n = (1.2403 + 0.5306)² / (0.0777)² = 519.6, rounded up to 520 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 <- 0.684210526315789                          # control proportion
p1 <- 0.761904761904762                          # 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(5405556)
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 = 520 (80% power), 696 (90% power)
 75% of observed effect: n per arm = 945 (80% power), 1,264 (90% power)
 50% of observed effect: n per arm = 2,168 (80% power), 2,902 (90% power)
power.prop.test: 519.6 
Simulated power at n = 520 per arm: 0.807 (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.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 17 outcome measures. Multiple outcomes create a multiplicity issue because repeated statistical testing can make chance findings more likely across a collection of comparisons. A prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory outcomes can help readers understand how results should be interpreted. The registry record does not report such a strategy.

The posted primary comparison has an unadjusted p-value of 0.583, and the secondary comparison has an unadjusted p-value of 0.342. These values do not account for other outcome testing. No reported analyses are listed for the secondary outcome, and the registry lists zero analyses. The registry record does not explain how the posted comparisons relate to the full set of outcome measures or whether additional analyses were planned.

Missing data and analysis populations are also important. The primary endpoint requires an eGFR measurement at the end of the four-week off-treatment period to determine whether a participant met the return-to-baseline criterion. The registry record does not report how missing or unusable measurements were handled. It also does not report whether the analyses included all randomized participants, only participants with an observed endpoint, or another analysis population.

Without that information, it is not possible to assess whether missing measurements could have changed the comparison or whether the analysis followed an intention-to-treat approach. The registry record also does not report a method for imputation, sensitivity analyses, or adjustment for baseline characteristics. These are unreported features of the record, not evidence that no such analyses were performed.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: central retinal vein occlusion (4.8%), deep venous thrombosis (4.8%), encephalocoele (4.8%).

The serious adverse event counts are 0 of 19 in the group assigned to report only study eGFR values more than 25% below baseline and 3 of 21 in the group assigned to report all study eGFR values. No deaths were recorded in either group. The registry also lists Central retinal vein occlusion, Deep venous thrombosis, and Encephalocoele among the top serious event terms, each with a reported value of 4.8%.

These counts are descriptive. With few serious events, they provide limited precision for comparing groups and do not establish that the reporting strategy caused or prevented an event. The registry record does not provide further event-level details, including timing, duration, or attribution, in the information summarized for this comparison.

Other adverse events were recorded in 11 of 19 participants in the restricted-reporting group and 15 of 21 in the all-results-reporting group. These figures should be read as recorded event counts within the study groups, not as a complete characterization of comparative safety. The trial's short observation period and modest group sizes limit the conclusions that can be drawn from rare or delayed events.

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

The primary result describes the proportion of participants who met the study's return-to-baseline eGFR criterion after the four-week off-treatment period, under two eGFR reporting strategies. More participants in the all-results-reporting group met that endpoint in the posted results, but the confidence interval is compatible with effects in either direction. The estimate is therefore uncertain rather than conclusive about the difference between strategies.

The trial does not compare sotagliflozin with placebo or with no treatment. The registry summary describes open-label sotagliflozin treatment, and randomization concerns how eGFR results were reported. The primary comparison should not be interpreted as a direct estimate of the drug's effect on eGFR or as proof that a reporting policy changes kidney function.

The endpoint reflects a specific measurement and time point: eGFR within plus or minus 10% of baseline at the end of the four-week off-treatment period. It does not by itself describe longer-term kidney function, transplant outcomes, or the experience of people outside the study population. The registry summary identifies adult kidney transplant recipients with stable allograft function; further details of the population are not reported in the registry record.

The results also do not establish that one communication strategy is preferable for clinical care. The posted comparisons are imprecise, and the record does not report the original sample-size justification, missing-data methods, analysis population, or multiplicity plan. These limitations constrain interpretation of both the primary and secondary outcomes. The findings are best understood as trial-specific observations that leave substantial uncertainty about the size and direction of differences between the randomized reporting strategies.

17. Why This Trial Matters Statistically

This trial is statistically notable because it randomizes an information and reporting policy while participants receive open-label treatment. The contrast is not a conventional drug-versus-placebo comparison. Separating the reporting strategy from the treatment question is essential for identifying what the primary estimate actually represents.

The endpoint also focuses on reversibility: it asks whether eGFR returns to a defined range around baseline after treatment stops. That design makes the timing of measurement central to interpretation. A binary endpoint can be straightforward to communicate, but the threshold turns a continuous measurement into a yes-or-no classification. The registry record does not report additional analyses of the underlying continuous eGFR values.

The comparison illustrates why an observed difference should be read together with its confidence interval. The primary point estimate favors one reporting group, but its interval crosses the no-difference value and spans both directions. The data are not precise enough to distinguish a benefit in one direction from little difference or an effect in the other direction.

Finally, the record makes the distinction between registered outcomes and reported analyses important. It lists 17 outcome measures but provides no reported secondary analyses and no detail about multiplicity or missing-data handling. Those omissions limit the ability to evaluate the full analysis strategy. The registry's enrollment entry and summary description also differ, without an explanation in the record. Transparent accounting of enrollment, analysis populations, and prespecified methods would help readers assess how much weight to place on the observed results.

18. Limitations

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

The number of participants in each randomized group is modest, so the primary and secondary estimates are imprecise. The primary confidence interval spans effects in either direction, limiting conclusions about the size or direction of the reporting-strategy contrast. Serious adverse event counts are sparse as well, so they do not support a precise comparison of uncommon safety outcomes.

The registry record contains an unresolved enrollment discrepancy: the enrollment entry is 40, while the brief summary describes N=50. The posted randomized groups contain 19 and 21 participants, but the record does not give a participant-flow explanation or identify the analysis population. This makes it difficult to trace the relationship between the summary, enrollment entry, and posted results.

The study is unmasked, and participants and providers were aware of the assigned eGFR reporting strategy. The registry record does not say whether outcome assessment was masked. Because the endpoint is based on an eGFR measurement, the record's lack of detail about measurement handling and missing endpoint data is relevant. The method for handling unavailable measurements is not reported in the registry record.

The follow-up period for the primary endpoint is 16 weeks total, with four weeks off treatment. The results therefore address the stated short-term assessment and do not establish longer-term patterns. The registry record also does not report the original sample-size justification, multiplicity approach, covariate adjustment, analysis population, or sensitivity analyses. These trial-specific omissions constrain assessment of the robustness and generalizability of the posted comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Sotagliflozin Safety and Tolerability Among Renal Transplant Recipients — NCT05405556.
• Registry record last updated 2026-11-04; status last verified 2026-10.
• Results first posted 2026-11-04.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT05405556 is a completed, randomized, unmasked, parallel-group phase 2 trial titled “Sotagliflozin Safety and Tolerability Among Renal Transplant Recipients.” The registry identifies eGFR reporting as the intervention and compares reporting only values more than 25% below baseline with reporting all study eGFR values.

The primary endpoint is return to within plus or minus 10% of baseline eGFR after 12 weeks of open-label treatment and four weeks off treatment. The posted counts are 13 of 19 and 16 of 21. The risk-difference interval spans effects in both directions, and the unadjusted p-value is 0.583.

The record lists enrollment as 40, while its brief summary describes N=50; it does not explain this discrepancy. The record also does not report the original sample-size justification, analysis population, missing-data handling, or multiplicity plan. The listed start date is 2022-10-17, and the primary completion date is 2024-05-10.