An Investigation Into the Effect of Dapagliflozin on Ketogenesis in Type 1 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Investigation Into the Effect of Dapagliflozin on Ketogenesis in Type 1 Diabetes (NCT02962492), a randomized na study. The primary outcome is Change in Beta-hydroxybutyrate Levels in Blood.

2. Clinical Question

The statistical question is whether the observed mean change differed between each active-treatment arm and placebo, and how precisely each difference was estimated. The posted arm summaries and recalculated contrasts describe variation in a laboratory measure; they do not by themselves establish why any group difference occurred or what it means for health. The record describes both acute single-dose assessments and longer-term treatment, while the posted primary outcome is framed as a comparison of the acute-stress change at week 12 with the change at week 0.

3. Trial Design

The registry describes a randomized, triple-masked, parallel study with an enrollment of 70. Its status is completed. The recorded study start is 2016-11-01, and the primary completion date is 2021-02-01. The phase is listed as NA, and the sponsor is the University at Buffalo.

The four posted arms are placebo, dapagliflozin, exenatide extended release, and the combination of exenatide extended release with dapagliflozin. The arm descriptions distinguish oral dapagliflozin from its oral placebo and subcutaneous exenatide or extended-release exenatide from its injection placebo. The brief description includes acute assessments after a single dose under insulinopenic conditions and longer-term assessment before and after 12 weeks of treatment under basal conditions. It describes evaluation of ketogenesis, glucagon, and lipolysis.

The primary outcome summaries include 11 participants in the placebo arm, 15 in the dapagliflozin arm, 15 in the exenatide extended release arm, and 21 in the combination arm. These are the participant counts attached to the posted outcome, rather than a description of the complete participant flow. Reasons for differences between those counts and the enrollment figure are not reported in the registry record.

Details of the randomization procedure, allocation concealment, masking roles, treatment adherence, and follow-up procedures are not reported in the registry record. The record also does not report the original sample-size justification or a full statistical analysis plan. Those omissions limit how specifically the design can be reconstructed, even though the basic randomized, masked, parallel structure and treatment groups are described.

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 Change in Beta-hydroxybutyrate Levels in Blood, measured over 12 weeks.

The primary endpoint is change in blood beta-hydroxybutyrate, abbreviated BHB, measured in mM. BHB is a ketone body, so its concentration is used in this study as a biochemical measure related to ketogenesis. The endpoint description specifies measurement during acute stress conditions in all groups after a single-dose intervention, with assessments at baseline (0 Week) and at 12 weeks of treatment.

At each visit, the change was calculated from that visit's baseline (0 hr). The posted primary outcome is then the change at week 12 minus the change at week 0. This contrast focuses on whether the acute-stress response differed after the treatment period from the response at the initial visit. It is not simply the BHB concentration at week 12, nor is it described as a direct measure of a clinical event.

Using a continuous laboratory measure can capture variation across participants and can be useful for evaluating a biological response. However, the registry record does not report a clinically meaningful threshold for this endpoint, explain how BHB changes relate to patient-important outcomes, or provide further detail about the stress protocol. The results should therefore be read as differences in a biochemical measure, not as direct evidence about symptoms, complications, or overall health.

7. Results Posted in the Registry

• Dapagliflozin Arm:: mean 0.63 versus -0.23 on control; difference 0.86 (95% CI 0.32 to 1.40), standardized effect d = 1.15; z-test p = 0.002.
• Exenatide Extended Release Arm:: mean 0.24 versus -0.23 on control; difference 0.47 (95% CI -0.06 to 1.00), standardized effect d = 0.65; z-test p = 0.082.
• Exenatide Extended Release & Dapagliflozin Arm:: mean 0.31 versus -0.23 on control; difference 0.54 (95% CI 0.04 to 1.04), standardized effect d = 0.69; z-test p = 0.034.

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.

Change in HbA1c Following Treatment

• 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:
  • Dapagliflozin Arm:: mean -0.30 versus -0.10 on control; difference -0.20 (95% CI -0.48 to 0.08), standardized effect d = -0.55; z-test p = 0.157.
  • Exenatide Extended Release Arm:: mean -0.40 versus -0.10 on control; difference -0.30 (95% CI -0.74 to 0.14), standardized effect d = -0.48; z-test p = 0.180.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dapagliflozin Arm: and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exenatide Extended Release Arm: and the control. The interval gives the range of effects that remain compatible with the data.

Change in Urinary Beta-hydroxybutyrate (BHB) After 12 Weeks of Treatment

• 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:
  • Dapagliflozin Arm:: mean 0.40 versus 1.20 on control; difference -0.80 (95% CI -1.86 to 0.26), standardized effect d = -0.65; z-test p = 0.137.
  • Exenatide Extended Release Arm:: mean -0.70 versus 1.20 on control; difference -1.90 (95% CI -3.43 to -0.37), standardized effect d = -0.92; z-test p = 0.015.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dapagliflozin Arm: and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Exenatide Extended Release Arm: than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Plasma Glucagon

• 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:
  • Dapagliflozin Arm:: mean 16.00 versus 2.00 on control; difference 14.00 (95% CI -5.99 to 33.99), standardized effect d = 0.47; z-test p = 0.170.
  • Exenatide Extended Release Arm:: mean -15.00 versus 2.00 on control; difference -17.00 (95% CI -33.16 to -0.84), standardized effect d = -0.71; z-test p = 0.039.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dapagliflozin Arm: and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Exenatide Extended Release Arm: than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the biological picture beyond the primary blood BHB measure. They include change in HbA1c, urinary BHB, plasma glucagon, and total insulin dose. The posted results include arm summaries and recalculated comparisons for HbA1c, urinary BHB, and plasma glucagon. A result for change in total insulin dose is not reported in the registry record.

Across the posted secondary outcomes, the arm patterns are not uniform: group means differ in direction and size across measures, and the reported confidence intervals and unadjusted p values reflect varying levels of uncertainty. This heterogeneity means the secondary outcomes do not simply duplicate the primary BHB finding. They offer related, but distinct, information about glycemic measures, urinary ketones, and glucagon. Their relationship to the primary result is descriptive; the record does not report a formal analysis tying changes in these measures together.

Some individual secondary comparisons have unadjusted intervals that exclude zero, while others do not. These comparisons are exploratory in the sense that the registry record does not provide a reported multiplicity strategy or a complete inferential plan for the secondary outcomes. When several outcomes and treatment contrasts are considered, isolated unadjusted p values carry less weight than a prespecified, multiplicity-aware analysis.

The secondary findings should therefore be considered alongside the primary result without being treated as independent confirmation. They can indicate which measures warrant further study, but they do not establish a coherent mechanism or clinical effect. Results for outcomes not posted, including total insulin dose, cannot be inferred from the other measures. The registry record does not report additional analyses that clarify whether differences in these secondary endpoints were expected, adjusted for baseline values, or clinically important.

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

• Change in HbA1c Following Treatment
• Change in Urinary Beta-hydroxybutyrate (BHB) After 12 Weeks of Treatment
• Change in Plasma Glucagon
• Change in Total Insulin Dose

9. Statistical Interpretation

10. Statistical Methods Explained

For a continuous outcome, the group mean is the average value among participants with posted data for that outcome. The primary summaries report means and standard errors. A standard error describes the estimated uncertainty in a group mean; it is not the same as the spread of individual participant measurements. General statistical explanation: a smaller standard error usually corresponds to a more precisely estimated mean, while a larger standard error signals greater uncertainty in that estimate.

What does a mean difference represent?

The posted contrasts compare each active-treatment arm's mean with the placebo mean. A positive mean difference indicates that the active-arm mean is higher than the placebo mean for the defined endpoint; a negative difference indicates that it is lower. For this primary outcome, the endpoint itself is the change at week 12 minus the change at week 0. The direction of a contrast therefore concerns this defined change measure, not the absolute BHB concentration at a visit.

The mean differences and confidence intervals in the comparisons are recalculated, unadjusted results based on the posted arm-level summaries. They are not described in the registry record as sponsor-reported analyses. The record lists no reported inferential analyses for the primary outcome. The recalculations should be regarded as a transparent descriptive aid, not as a substitute for an analysis specified in a protocol. The discrepancy flag is false, so there is no recorded conflict between a recalculation and a sponsor analysis.

How should the p values be read?

A p value describes how unusual the observed data, or data more extreme, would be under a statistical model in which the groups have no mean difference. It is not the probability that a treatment has no effect, and it does not measure the size or clinical importance of a difference. The primary comparisons have unadjusted p values of 0.002, 0.082, and 0.034. Because they are unadjusted, they do not reflect a correction for considering multiple treatment comparisons or multiple outcomes.

General statistical explanation: repeated testing creates more opportunities for apparently notable results to arise by chance, even if every null hypothesis is true. A multiplicity procedure can control a chosen error rate across a defined family of tests, but the registry record does not report such a procedure. The reported p values should therefore be read as individual, unadjusted comparisons rather than as a family-wise conclusion.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimated mean difference. Under the statistical method used to construct it, an interval gives a range of values compatible with the observed data and its assumptions. It does not mean that there is a stated probability that the fixed true difference lies within this particular interval. Intervals that are wide indicate less precision than narrow intervals. An interval that includes zero is compatible with no mean difference as well as with differences in either direction at the stated confidence level.

The primary confidence intervals are calculated from the posted summaries. They show different degrees of precision across the three active-versus-placebo contrasts. The registry record does not report a model-based adjustment for baseline values, stratification factors, or other covariates. No adjustment should be assumed from the randomized design alone.

Why can outcome variability matter?

General statistical explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. If it is ignored, standard errors and p values can be misleading. The posted primary results provide standard errors, but the registry record does not report a diagnostic assessment of distributional assumptions or an over-dispersion adjustment. There is no basis to infer from these summaries alone whether such an issue arose.

The planning illustrations use the observed effect as a reference and show participant requirements under specified hypothetical assumptions. They are not the original trial design calculation, because the trial's own design assumptions and sample-size justification are not reported in the registry record. They also do not represent observed power. The illustrations are most useful for showing how assumed effect size and target power affect planning, rather than for judging whether the completed trial was adequately powered.

These distinctions matter because the registry includes both posted summaries and recalculated comparisons. Group means describe the observed data; standard errors and confidence intervals describe precision; p values describe compatibility with a null model; and planning figures describe hypothetical future design scenarios. None alone answers whether a change is clinically important. That judgment would require context about the measure's meaning and a clinically interpretable threshold, which are not reported in the registry record.

11. Confidence Intervals and Precision

The primary mean differences are accompanied by confidence intervals, which make the uncertainty visible rather than presenting a point estimate alone. The dapagliflozin comparison has an estimated difference of 0.86 mM and a 95% confidence interval from 0.315 to 1.405. The exenatide extended release comparison has an estimated difference of 0.47 mM and an interval from -0.059 to 1.000. The combination comparison has an estimated difference of 0.54 mM and an interval from 0.040 to 1.04.

The exenatide extended release interval includes zero, so the posted data are compatible with no mean difference as well as with values on either side of zero under the recalculation method. The intervals for dapagliflozin and the combination lie above zero. That distinction is about the estimated direction and statistical uncertainty; it does not establish that the differences are clinically meaningful, nor does it account for multiplicity.

The arm sizes attached to the primary outcome are 11, 15, 15, and 21. With limited outcome-group counts, estimates can be sensitive to individual observations, and uncertainty may remain substantial. The standard errors are reported for group means, not as a description of the full distribution of participant values. The registry record does not report raw observations or additional distributional summaries that would allow a fuller assessment of variability.

Confidence intervals are conditional on the method and assumptions used to calculate them. These are recalculated unadjusted intervals from posted summary statistics; the registry record does not report sponsor-generated intervals or a prespecified adjustment strategy. The intervals are therefore best used to understand the approximate precision of the posted comparisons, not to imply a complete confirmatory analysis. No threshold for a clinically important BHB difference is reported in the registry record, so statistical precision cannot be translated into clinical importance.

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 for 80% power and participants per arm for 90% power. They are not total event counts: this is a continuous-outcome analysis, and the planning values are expressed per arm. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect.

The 80% power column gives the hypothetical number of participants per arm for a design with an 80% chance of detecting the assumed effect under the planning model, if that effect and the model assumptions were correct. The 90% power column describes the corresponding design target with a 90% chance. These are design probabilities under assumptions, not probabilities that the observed result is true. The trial's original sample-size justification and its own planning assumptions are not reported in the registry record.

Rows that plan for 75% or 50% of the observed effect use smaller assumed differences than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the assumed effect becomes smaller. The values vary by comparison because the observed effect and variability differ across the posted outcomes.

These calculations are planning illustrations based on observed summaries, not observed power. They should not be read as evidence that the completed study had a particular probability of finding an effect. Nor do they account for unreported design features, missing data, multiplicity, or any analysis plan that may have been used outside the registry record. Their value is to show how sample-size requirements depend on the assumed effect and target power, not to retrospectively certify the trial design.

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 = 0.860; pooled standard deviation σ = 0.746.
2. n = 2 × (1.96 + 0.842)² × 0.746² / 0.860² = 11.8, rounded up to 12 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 <- 0.86                      # observed difference in means
sigma <- 0.745626135092738                     # 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(2962492)
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 = 12 (80% power), 16 (90% power)
 75% of observed effect: n per arm = 21 (80% power), 29 (90% power)
 50% of observed effect: n per arm = 48 (80% power), 64 (90% power)
power.t.test: 12.8 
Simulated power at n = 12 per arm: 0.774 (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 lists a primary outcome and several secondary outcomes, with comparisons among multiple active-treatment arms and placebo. It does not report how the investigators defined families of hypotheses or whether they adjusted for multiple comparisons. The p values associated with the recalculated comparisons are unadjusted. Without a stated multiplicity plan, they should not be interpreted as controlling the overall chance of a false-positive finding across all outcomes and contrasts.

The record does not report a full statistical analysis plan, the timing of its finalization, any interim analyses, or whether additional analyses were conducted but not posted. The registry's reported-analyses count is 0. That absence means the posted summaries and recalculations do not establish which analyses were prespecified, which were exploratory, or whether the analysis methods were changed. Those details are not reported in the registry record.

Missing-data handling is also not reported in the registry record. The posted outcome counts differ across arms, but reasons for the outcome counts, participant withdrawals, missing measurements, or the handling of missing observations are not described. The analysis population is not identified as intention-to-treat, per-protocol, or another defined set. It is therefore not possible to determine from the record whether all randomized participants were included in each analysis or how missing data could have affected the estimates.

Details about baseline adjustment, covariates, model diagnostics, distributional assumptions, and sensitivity analyses are not reported. These omissions do not show that such methods were absent from the conduct of the study; they mean that the registry record does not document them. A complete interpretation of confirmatory evidence would require the prespecified analysis approach, the participant flow, and a clear account of missing observations and multiplicity handling.

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.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: severe hypoglycemia (0.0%), diabetic ketoacidosis (0.0%).

The posted serious adverse event summaries report zero affected participants in each arm: placebo, dapagliflozin, exenatide extended release, and the combination. The numbers at risk for these summaries are 11, 15, 15, and 21, respectively. The record also lists Severe Hypoglycemia and Diabetic Ketoacidosis among serious adverse event terms, each at 0.0%.

These figures describe what was recorded in the registry for the reported groups; they do not show that no adverse events of any kind occurred. The summaries distinguish serious adverse events from other adverse events, and the posted counts for other adverse events are also zero in each arm. The study's modest arm sizes and the absence of further event detail limit the conclusions that can be drawn from zero recorded events.

The registry record does not provide additional context about event definitions, collection procedures, exposure time, or the completeness of adverse-event reporting. Zero reported events in this study should not be interpreted as proof that an intervention cannot cause an event, or as a comparison of safety across treatments. The figures are a description of the registry's posted safety record, not medical advice or a definitive assessment of risk.

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

The primary results describe differences between treatment-arm means in a specific biochemical endpoint: the change in acute-stress blood BHB at week 12 compared with the change at week 0. The recalculated contrasts are positive for each active arm versus placebo. The confidence intervals indicate that the estimates have varying precision, and the exenatide extended release interval includes zero. These observations characterize the posted data under an unadjusted comparison; they are not a complete analysis of all the study's design features.

The result does not establish that a treatment improves or worsens health. The registry record does not report a clinically important threshold for BHB, patient-reported outcomes, or clinical-event results that would connect the biochemical changes to how participants feel or function. A laboratory difference can be statistically distinguishable from zero without being clinically meaningful. Conversely, an uncertain estimate does not prove that no difference exists.

The trial includes a placebo arm and randomized, triple-masked, parallel assignment, which are relevant design features for comparing groups. But interpretation also depends on the randomization details, analysis population, missing-data handling, outcome methods, and prespecified statistical plan. Several of those details are not reported in the registry record. The posted recalculations therefore should not be substituted for a full protocol-based analysis.

The secondary results add context but do not resolve these limitations. They cover related metabolic measures, yet the registry does not report a multiplicity approach, a complete analysis plan, or a posted result for total insulin dose. Likewise, the zero serious adverse event counts are limited observations, not evidence that risk is absent.

The most defensible conclusion is descriptive: the registry reports differing mean changes in blood BHB across the treatment arms, with confidence intervals that express uncertainty and unadjusted p values that do not account for the full set of comparisons. Clinical significance, causal mechanisms, and implications for treatment decisions are not established by these registry summaries alone.

17. Why This Trial Matters Statistically

This study is statistically instructive because it combines several active treatment strategies, a placebo comparator, acute assessments, and a longer treatment period while focusing on a continuous biochemical measure. The primary outcome is not a simple endpoint value; it contrasts acute-stress change after 12 weeks with acute-stress change at week 0. That definition matters because interpretation depends on understanding exactly which change is being compared.

The posted results also show why point estimates should be read with uncertainty. The active-versus-placebo estimates vary in precision, and an unadjusted p value cannot replace a confidence interval or describe clinical importance. With several arms and secondary outcomes, multiplicity is relevant, yet its handling is not reported in the registry record. The recalculated summaries can illustrate the data while leaving the confirmatory status of individual comparisons unresolved.

The planning illustrations help distinguish retrospective effect-size-based planning from the original trial design. They show that required sample sizes depend on the effect a future study aims to detect and its target power. Because the original justification is not reported, the illustrations cannot explain why the study enrolled its participants or establish the adequacy of that enrollment.

Finally, this record highlights the importance of transparent reporting. Participant flow, missing-data methods, analysis populations, and a full statistical plan affect how results should be interpreted. Their absence from the registry record does not imply that no such methods were used, but it does limit independent assessment. This is a useful reminder that estimates, precision, design, and reporting completeness all contribute to the strength of a statistical conclusion.

18. Limitations

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

Several limitations are specific to the information recorded for this study. The participant population is not described beyond the condition label and the study's focus on ketogenic stress. Eligibility criteria, participant characteristics, and the precise context of insulinopenic and basal conditions are not reported in the registry record. Those details would help readers judge the scope to which the results apply.

The outcome definition refers to acute stress conditions, but the registry record does not report the full stress protocol, timing details beyond the endpoint description, or procedures for measuring BHB. The primary outcome combines within-visit changes and then contrasts those changes across visits. Without further protocol detail, it is difficult to assess how reproducible or clinically interpretable that measure is.

Outcome-group counts are limited and vary by arm. The record does not explain participant flow or why the posted counts differ from the enrollment figure. Missing-data methods and analysis populations are not reported, so the possibility of bias from incomplete observations cannot be evaluated from the registry alone. No raw participant-level data or additional distributional summaries are posted in the registry record of this study.

The comparisons are recalculated from posted summary statistics rather than reported inferential analyses. The registry record does not report model specifications, baseline adjustment, multiplicity handling, or sensitivity analyses. The secondary outcome for total insulin dose has no posted result. The record also does not give a clinically meaningful threshold for the primary endpoint. These gaps constrain both statistical and clinical interpretation without establishing that the trial itself lacked additional analyses or procedures.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: An Investigation Into the Effect of Dapagliflozin on Ketogenesis in Type 1 Diabetes — NCT02962492.
• Registry record last updated 2024-02-29; status last verified 2024-02.
• Results first posted 2024-02-29.
• 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

NCT02962492 is a completed randomized, triple-masked, parallel study sponsored by the University at Buffalo, with enrollment of 70. It evaluated dapagliflozin, exenatide or exenatide extended release, their combination, and placebo in relation to ketogenesis and other metabolic measures. The primary endpoint was change in blood beta-hydroxybutyrate during acute stress, comparing the change at 12 weeks with the change at week 0.

The posted primary summaries show positive unadjusted mean differences for each active arm versus placebo, with differing confidence-interval precision. These comparisons are recalculated from arm summaries; the registry record reports no inferential analyses or multiplicity method. Secondary measures provide additional but incomplete context, and a result for total insulin dose is not reported in the registry record. Serious adverse event counts are zero in all posted arms, but this does not establish absence of risk. Important details about missing data, analysis populations, and the original sample-size justification are not reported in the registry record.