SGLT2 Inhibition in Older Obese Adults With Pre-diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SGLT2 Inhibition in Older Obese Adults With Pre-diabetes (NCT04401904), a randomized phase 1, phase 2 study. The primary outcome is AGE-RAGE Measurement in Plasma.

2. Clinical Question

3. Trial Design

This completed study is listed as a randomized, parallel-group trial with no masking and a PHASE1/PHASE2 designation. The registry record gives an enrollment of 20. The arm descriptions specify 10 participants assigned to dapagliflozin and 10 to nutritional counseling. The study compares the groups over 12 weeks, with the primary outcome measured as change from baseline.

Participants in the experimental group were assigned dapagliflozin 10 mg by mouth daily. Participants in the comparator group were assigned weekly nutritional counseling. The registry record identifies both a drug and a behavioral intervention, but does not give additional details about adherence monitoring, treatment discontinuation, or the content and delivery of the counseling.

The primary outcome is plasma AGE-RAGE measurement by enzyme-linked immunosorbent assay (ELISA). The registry record also posts changes in grip strength and 6 Minute Walking Distance as secondary outcomes. It reports means and standard errors for the groups, as well as unadjusted comparisons. Confidence limits are available for the mean differences. The record does not provide a fuller account of the statistical analysis procedures or identify the populations included in each analysis.

The study is marked completed. Its start date is 2020-06-25 and its primary completion date is 2022-09-14. These dates describe the registry timeline; they do not, by themselves, provide information about the duration of follow-up beyond the stated 12-week outcome timeframe or about the timing of individual participant assessments. The original design assumptions and the rationale for selecting the enrollment target are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

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 AGE-RAGE Measurement in Plasma, measured over Baseline to 12 weeks.

The primary endpoint is the change in plasma AGE-RAGE measurement from baseline to 12 weeks, expressed in pg/mL. The registry describes the measurement as made by ELISA, a laboratory assay used to quantify a target in a sample. The reported outcome is a continuous measure, and the posted summaries use group means with standard errors.

The endpoint is relevant to the study’s stated rationale because the investigators hypothesized that SGLT2 inhibition could affect aging-related processes, including advanced glycation end products (AGE) and the receptor for AGE (RAGE). The registry’s rationale also discusses oxidative damage, cellular senescence, and mitochondrial function, but the primary outcome posted is specifically the AGE-RAGE plasma measurement. A measured change in this biomarker is not itself a direct measure of aging as a whole, nor does it establish the mechanism responsible for a change.

Using a change from baseline focuses the outcome on how the measured value shifted during the stated period. Comparing average changes between randomized groups can describe the difference in those shifts. The registry does not report further details about the assay’s measurement properties, the separate contributions of AGE and RAGE to the reported measurement, or a threshold defining a meaningful change. Those details are not reported in the registry record, so the numerical result should be read as a difference in the posted continuous outcome rather than as a clinical interpretation of the biomarker.

7. Results Posted in the Registry

• Nutritional Counseling: mean -86.00 versus -172.00 on control; difference 86.00 (95% CI -237.16 to 409.16), standardized effect d = 0.23; z-test p = 0.602.

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.

Grip Strength

• 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 errors.
• Result:
  • Nutritional Counseling: mean -1.00 versus -2.00 on control; difference 1.00 (95% CI -2.47 to 4.47), standardized effect d = 0.25; z-test p = 0.572.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nutritional Counseling and the control. The interval gives the range of effects that remain compatible with the data.

6 Minute Walking Distance

• 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 errors.
• Result:
  • Nutritional Counseling: mean 9.10 versus 6.60 on control; difference 2.50 (95% CI -25.01 to 30.01), standardized effect d = 0.08; z-test p = 0.859.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nutritional Counseling and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add functional measures to the primary biomarker result: grip strength and 6 Minute Walking Distance. Across these outcomes, the posted mean changes are not identical between groups, but the estimated differences are uncertain. Both secondary confidence intervals include zero, and both unadjusted p-values are relatively large. This overall pattern does not provide a precise or consistent basis for claiming a clear separation between the assigned groups on the secondary measures.

These results relate to the primary finding by offering additional outcome information over the same baseline-to-12-week timeframe. They do not directly validate the AGE-RAGE measure or explain any change in it. Functional measures and a plasma biomarker represent different kinds of outcomes, and agreement or disagreement among them would not by itself establish a biological mechanism. The secondary findings should be considered alongside, rather than as substitutes for, the primary comparison.

The registry record does not report a multiplicity adjustment for the secondary comparisons. General statistical explanation: when many outcomes or comparisons are tested, the chance of at least one apparently unusual result can increase, even when no underlying group effects exist. Adjusting for multiple testing can address that concern, but it may also change how much evidence is required for an individual comparison. Without a reported adjustment plan, the secondary p-values are best treated as unadjusted and exploratory.

The number of participants is limited, and the registry does not report a prespecified hierarchy or detailed analysis plan for these outcomes. That makes it difficult to determine whether the secondary outcomes were intended as confirmatory tests or primarily descriptive measures. Their estimates can guide interpretation of the posted result pattern, but they carry less weight than a prespecified, adequately powered confirmatory analysis with a documented multiplicity strategy. These results should not be used to make broader claims about functional change beyond the measures and timeframe recorded.

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

• Grip Strength
• 6 Minute Walking Distance

9. Statistical Interpretation

10. Statistical Methods Explained

For a continuous outcome, a group mean describes the average observed change among the participants included in that summary. The posted primary endpoint is a mean change in pg/mL, not a count or a proportion. A negative mean change indicates that the average measured value moved downward from baseline; it does not mean that every participant’s measurement decreased. Individual participant results are not reported in the registry record.

What does the standard error describe?

The registry reports standard errors alongside the group means. General statistical explanation: a standard error describes the uncertainty in an estimated mean, rather than the spread of individual observations. It tends to be smaller when an estimate is based on more information and larger when the underlying observations are more variable. A standard error should not be read as though it were the range of values experienced by participants. The registry does not post the individual-level distributions or standard deviations for these outcomes.

The primary group standard errors are 121.0 pg/mL for dapagliflozin and 112.0 pg/mL for nutritional counseling. The comparator estimate is formed from the difference between group means. Its uncertainty depends on the precision of both group estimates. The registry posts the mean difference and its confidence interval directly, so those are the most useful quantities for interpreting the estimated contrast and its precision.

How should the group difference be read?

The comparison is expressed as nutritional counseling minus dapagliflozin. For the primary result, the posted means are -172.0 pg/mL and -86.0 pg/mL, respectively, and the reported difference is 86.0 pg/mL. This direction means that the nutritional-counseling mean change is higher, or less negative, than the dapagliflozin mean change. The comparison describes an average contrast; it does not describe the change for a typical participant or the range of individual responses.

The registry also gives unadjusted p-values. General statistical explanation: a p-value measures how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The primary unadjusted p-value is 0.602. The registry record does not report enough detail about the test procedure to reconstruct the full analysis plan, including any covariate adjustment or handling of deviations from assumptions.

What does a confidence interval add?

General statistical explanation: a confidence interval gives a range of values compatible with the observed data under the interval’s statistical assumptions. It communicates uncertainty in the estimated group difference more directly than a point estimate alone. The primary interval runs from -237.2 to 409.2 pg/mL. Because it includes zero and also spans differences in either direction, it indicates substantial uncertainty about the direction and size of the group contrast. The interval should not be interpreted as a range containing all participant changes.

Random assignment is intended to support a fair comparison of groups by reducing systematic differences in treatment assignment. The registry identifies the allocation as randomized, but does not report the sequence-generation method, allocation concealment, or details of how randomization was implemented. No masking is listed. The record does not give the original statistical plan, the analysis population definition, or details about the model used to produce the posted comparisons. These aspects of the methods are therefore not reported in the registry record.

Why does over-dispersion matter?

General statistical explanation: over-dispersion occurs when observations vary more than a statistical model assumes. When a model understates variability, standard errors may be too small and confidence intervals too narrow; the resulting test statistics can appear more decisive than the data warrant. This concept is relevant to statistical modeling broadly, but the posted outcomes are continuous means and the registry does not report an over-dispersion assessment or a model-based diagnostic. There is no basis in the record to claim that over-dispersion was present or that it affected these estimates.

The registry’s numerical summaries are enough to describe the reported group means, differences, confidence limits, and unadjusted p-values. They are not enough to independently verify every analytic decision or determine how incomplete observations were treated. The record also does not report whether any interim analyses were conducted, how missing data were handled, or whether outcomes were analyzed according to randomized assignment. General methodological considerations should not be mistaken for a description of procedures that the registry does not document.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the available data. The primary mean difference is 86.0 pg/mL, but its confidence interval extends from -237.2 to 409.2 pg/mL. This interval is broad relative to the point estimate and includes zero as well as differences in both directions. It therefore leaves considerable uncertainty about the size and direction of the between-group contrast. The registry does not report a clinical threshold for interpreting the importance of a difference in this biomarker.

A confidence interval is not a prediction interval for individual participants, nor does it show the range of all possible study results. General statistical explanation: under the assumptions used to construct it, a confidence interval represents a range of values compatible with the observed data and method. The exact construction method is not reported in the registry record, so the posted limits should be understood as the registry’s stated interval rather than as a fully reproducible analysis specification.

The primary estimate is based on 10 participants in each arm. The small group sizes provide limited information for estimating a mean difference, which is consistent with the substantial uncertainty visible in the interval. The unadjusted p-value of 0.602 is another summary of the evidence under a null model, but it does not replace the interval: it cannot show the range of differences that remain compatible with the data.

The secondary confidence intervals are also wide: the grip-strength difference has limits from -2.468 to 4.468 Nm, and the 6 Minute Walking Distance difference has limits from -25.01 to 30.01 m. These intervals likewise include zero and allow uncertainty in either direction. Taken together, the posted results are more informative about the limitations of precision than about a narrowly determined group effect. A larger sample could yield greater precision, but the registry’s planning illustrations are not the original design justification and do not guarantee a particular future result.

12. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the displayed figures are participants per arm, not total events. The planning assumptions listed in the registry are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm estimated to be needed for an 80% chance of detecting the specified effect under those planning assumptions, if that effect is truly present. The 90% power column gives the corresponding estimate for a 90% chance. These are planning concepts: power is the probability that a study with a specified design will detect an effect of a specified size under the assumed model. The original trial’s own sample-size justification and design assumptions are not reported in the registry record.

The rows consider planning for 100%, 75%, and 50% of the observed effect. The displayed requirements increase as the target effect becomes smaller. For example, primary-outcome planning for 75% of the observed effect gives 513 participants per arm for 80% power and 687 participants per arm for 90% power; planning for 50% gives 1,154 and 1,545 participants per arm, respectively. Smaller effects are harder to distinguish from random variation, so more participants are needed under these assumptions.

These calculations are illustrations, not observed power. They do not show the probability that the completed trial’s result is correct, nor do they establish what sample size would be appropriate for a future study without considering its research question and design. The estimates rely on the observed effect as a planning reference, which may itself be uncertain in a small trial.

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 = 86.000; pooled standard deviation σ = 368.680.
2. n = 2 × (1.96 + 0.842)² × 368.680² / 86.000² = 288.5, rounded up to 289 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 <- 86                      # observed difference in means
sigma <- 368.680078116516                     # 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(4401904)
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 = 289 (80% power), 387 (90% power)
 75% of observed effect: n per arm = 513 (80% power), 687 (90% power)
 50% of observed effect: n per arm = 1,154 (80% power), 1,545 (90% power)
power.t.test: 289.5 
Simulated power at n = 289 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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity-adjustment procedure, a hierarchy among outcomes, or a detailed statistical analysis plan. It lists a primary outcome and two secondary outcomes, but does not describe how the investigators intended to manage the possibility of multiple statistical comparisons. This matters because the interpretation of several unadjusted tests differs from the interpretation of one prespecified primary test: considering many outcomes can increase the chance of a nominally notable result arising by chance.

The posted p-values are identified as unadjusted. The primary comparison has an unadjusted p-value of 0.602; the secondary comparisons have unadjusted p-values of 0.572 and 0.859. These values should not be treated as multiplicity-adjusted evidence. The registry does not report whether additional comparisons were conducted but not posted, or whether any other correction was used outside the displayed results.

Missing-data handling is also not reported in the registry record. The arm summaries list 10 participants per group, but the record does not specify whether all randomized participants contributed data to each endpoint, whether any measurements were missing, or how incomplete follow-up was handled. A listed group size alone cannot establish that every participant had a complete outcome assessment. The record does not describe imputation, exclusion criteria for analyses, or sensitivity analyses for missing observations.

Analysis populations are not described. In particular, the registry does not state whether the comparisons followed randomized assignment for all participants, used only participants who completed treatment, or used another analysis population. Nor does it report how adherence, treatment discontinuation, or protocol deviations were addressed. These omissions limit assessment of whether the posted estimates preserve the advantages of randomization and whether the analyzed groups correspond to the randomized groups.

The registry also does not report whether interim analyses were conducted or how any such analyses might have affected statistical interpretation. No conclusions about interim monitoring, missing-data procedures, or analysis-population choices can be drawn from the posted record. These are reporting gaps, not evidence that a particular procedure was or was not used in practice.

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 5% reporting threshold.

The registry reports 10 participants at risk for serious adverse events in each group. Serious adverse events affected 0 in the dapagliflozin group and 0 in the nutritional-counseling group. Other adverse events affected 0 of 10 at risk in each group, and deaths were 0 in both groups. No serious adverse-event terms are listed.

These are counts from a trial with 10 participants per arm and a 12-week outcome timeframe. They describe what the registry record reports for these groups and this study period. They do not establish that an event could not occur, provide a precise estimate of the frequency of uncommon events, or demonstrate equivalence in safety between the groups. The record does not provide further detail about adverse-event definitions, how events were collected, or the timing and severity of events beyond the serious and other categories reported.

Safety counts should be read alongside the small enrollment and the limits of the recorded follow-up. They are descriptive figures, not a comprehensive characterization of risk in other populations or over longer periods.

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

The result describes the average change in plasma AGE-RAGE measurement over 12 weeks in two randomized groups: one assigned dapagliflozin and the other weekly nutritional counseling. The estimated difference between group means is 86.0 pg/mL, with a confidence interval from -237.2 to 409.2 pg/mL. The interval is broad and includes differences in either direction. The estimate and its uncertainty are more informative together than either the point estimate or the p-value alone.

The data do not establish that the groups had the same average change. A nonzero difference could be compatible with the interval, and the study’s small enrollment leaves substantial uncertainty. Conversely, the point estimate does not establish that one group had a reliable or clinically meaningful advantage. The registry does not report a threshold for meaningful change in the biomarker, and the posted data do not resolve the uncertainty.

The study’s rationale connects SGLT2 inhibition with several proposed aging-related processes. The primary result is a measurement of one plasma outcome, not a direct test of every process in that rationale. It does not by itself establish an effect on aging, cellular senescence, mitochondrial function, oxidative damage, or other outcomes not reported. Nor does it show what caused the observed group means.

The trial compares dapagliflozin with nutritional counseling, not with an untreated or placebo group. The registry identifies the trial as randomized but not masked. Results should be interpreted within that design and the stated timeframe. They cannot establish what would happen under a different comparator, treatment duration, participant group, or measurement schedule.

Nothing in these posted estimates alone establishes effects on clinical outcomes beyond the endpoints listed. The functional secondary outcomes are uncertain, and the registry does not report enough detail about missing data, adherence, analysis populations, or multiplicity procedures to resolve those methodological questions. The result is best understood as an imprecise estimate of a group difference in a particular biomarker change, with additional exploratory information from two functional outcomes.

17. Why This Trial Matters Statistically

Statistically, the trial illustrates the distinction between an estimated effect and the precision of that estimate. The primary point estimate is a single number, but the confidence interval is wide and spans possible differences in either direction. Readers who focus only on the point estimate or on whether a p-value crosses a threshold would miss how much uncertainty remains in the comparison.

The study also shows why small randomized trials can be useful for describing measured outcomes while remaining limited for precise between-group estimates. The registry reports 20 participants in total, with 10 per arm. The planning illustrations based on observed effects require much larger per-arm numbers under the stated assumptions, especially when planning around a smaller fraction of the observed effect. Those illustrations are not the original design rationale, but they make visible how demanding a precise comparison can be when the observed effect is modest relative to variability.

A further statistical point is that a biomarker hypothesis and a biomarker result are not the same as evidence about every related biological process. The trial’s rationale gives context for why AGE-RAGE was measured; the endpoint remains a specific continuous measure over a specified period. The other reported outcomes broaden the description but do not prove that one outcome explains another.

Finally, interpretation depends on reporting. Details about analysis populations, missing data, multiplicity, and the original sample-size rationale are not reported in the registry record. Their absence limits independent evaluation of the analysis and the strength of conclusions that could be drawn from it. The record is most useful when its estimates, uncertainty, design scope, and reporting gaps are considered together.

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 most immediate limitation is the small enrollment: the registry lists 20 participants, with 10 assigned to each group. This leaves limited information for estimating group means and their difference, as reflected in the broad primary confidence interval. The planning illustrations further show that even planning around the observed effect leads to substantially larger per-arm requirements under the stated assumptions. Those calculations should not be mistaken for the trial’s own design justification.

The study is listed as having no masking. The record does not describe masking of outcome assessors or laboratory staff separately. It also does not report the method used to generate or conceal the randomization sequence. These details are relevant to evaluating potential sources of bias, but their absence from the registry record does not establish how procedures were conducted beyond what is listed.

Other trial-specific details are not reported in the registry record: participant age range and baseline characteristics; inclusion and exclusion criteria; counseling content; adherence; treatment discontinuation; and details of the laboratory assay beyond its identification as ELISA. Information about missing observations, analysis populations, covariate adjustment, and sensitivity analyses is also not reported. These omissions limit assessment of representativeness and analytic robustness.

The primary outcome concerns a plasma biomarker measured over 12 weeks. The record does not give a clinical threshold for interpreting the magnitude of its change. The two secondary measures add information but have uncertain comparisons, and no multiplicity strategy is reported. In addition, the safety counts come from a small group and a limited study timeframe, restricting what can be inferred about uncommon events or longer-term safety.

These limitations do not negate the posted results, but they narrow what those results can support. They are descriptive estimates from this trial’s randomized groups and specified outcome period, not a complete account of the intervention’s effects in other settings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: SGLT2 Inhibition in Older Obese Adults With Pre-diabetes — NCT04401904.
• Registry record last updated 2024-01-05; status last verified 2024-01.
• Results first posted 2024-01-05.
• 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

NCT04401904 is a completed randomized, parallel-group trial listed as PHASE1 and PHASE2, with no masking and enrollment of 20. It compares dapagliflozin 10 mg by mouth daily with weekly nutritional counseling over 12 weeks in older obese adults with pre-diabetes.

The primary outcome is change in plasma AGE-RAGE measurement from baseline to 12 weeks. The posted mean difference is 86.0 pg/mL, with a confidence interval from -237.2 to 409.2 pg/mL and an unadjusted p-value of 0.602. Grip strength and 6 Minute Walking Distance are also reported as secondary outcomes, with uncertain between-group comparisons.

The record reports 0 serious adverse events, 0 other adverse events, and 0 deaths in each group. Details about the original sample-size rationale, missing-data handling, analysis populations, and multiplicity procedures are not reported in the registry record.