A Study of Insulin Efsitora Alfa (LY3209590) Compared to Degludec in Adults With Type 2 Diabetes Who Are Starting Basal Insulin for the First Time: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Insulin Efsitora Alfa (LY3209590) Compared to Degludec in Adults With Type 2 Diabetes Who Are Starting Basal Insulin for the First Time (NCT05362058), a randomized phase 3 study. The primary outcome is Change From Baseline in HbA1c at Week 52 [Noninferiority Analysis].

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, parallel-design, open-label study comparing insulin efsitora alfa with insulin degludec. The registry record lists enrollment of 928 and describes adults with type 2 diabetes who were initiating basal insulin for the first time. The study is marked completed.

Participants assigned to the efsitora alfa group received 500 U/mL by subcutaneous injection once weekly. Participants assigned to the degludec group received 100 U/mL by subcutaneous injection once daily. Both treatment descriptions specify a 52-week treatment period followed by a 5-week safety follow-up. The study summary also describes a 1-week screening period and a 2-week lead-in period, and says the study would last up to 60 weeks.

The arm descriptions state that participants continued protocol-specified stable therapy with non-insulin antihyperglycemic medications. The descriptions available in the registry record are truncated, so further details about those medications or their management are not reported in the registry record. The trial had no masking, so participants and study personnel were not blinded to assigned treatment. Randomization can reduce systematic differences between groups at assignment, while open-label conduct may still affect treatment behavior, reporting, or assessment.

The primary endpoint was change from baseline in HbA1c at Week 52, analyzed as a noninferiority comparison. The registry record lists additional outcomes related to HbA1c, time in a blood-glucose range, fasting blood glucose, and glucose variability. The original sample-size justification, the planned noninferiority margin, and any interim analyses 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.

Before assignment: Participants continued their protocol-specified stable therapy with 1 to 3 non-insulin antihyperglycemic medications, including glucagon-like peptide-1 receptor agonists (GLP-1 RA), as well as non-GLP-1 receptor agonists such as dipeptidyl peptidase-4 (DPP-4) inhibitors, sodium-glucose cotransporter 2 (SGLT2) inhibitors, biguanides (e.g., metformin), alpha-glucosidase inhibitors, sulfonylureas (SUs), or thiazolidinediones throughout the study, at the discretion of the investigator.

Treatment Period

Reasons for not completing this period:

Follow-Up Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least one dose of the study drug and had HbA1c measurement at baseline or Week 52. Participants who discontinued the study drug due to inadvertent enrollment were excluded.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in HbA1c at Week 52 [Noninferiority Analysis], measured over Baseline, Week 52.

The primary endpoint was change from baseline in HbA1c at Week 52. HbA1c is the glycosylated fraction of hemoglobin A and is used as a measure of average plasma glucose concentration over a prolonged period. Because it reflects glucose over time rather than a single measurement, it can provide a summary of glycemic status during the treatment period.

The endpoint is expressed as a percentage of HbA1c. The registry reports least-squares means, which are model-adjusted group estimates rather than simple raw averages. The reported model was an analysis of covariance, or ANCOVA, with baseline HbA1c, country, GLP-1 receptor agonist use at randomization, sulfonylurea use at randomization, and treatment among its variables.

The primary analysis was designated as a noninferiority analysis. In general, a noninferiority analysis asks whether the difference between treatments is sufficiently limited according to a prespecified margin. That margin is needed to interpret the formal noninferiority conclusion, but it is not reported in the registry record. The endpoint and analysis therefore describe the comparison being made, while the posted estimates alone do not reveal the study’s decision threshold.

7. Results Posted in the Registry

• 100 U/mL - Insulin Degludec: mean -1.17 versus -1.26 on control; difference 0.09 (95% CI -0.04 to 0.22), standardized effect d = 0.09; z-test p = 0.177.

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 From Baseline in HbA1c at Week 52 in Participants Using GLP-1 Receptor Agonists [Noninferiority Analysis]

• 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:
  • 100 U/mL - Insulin Degludec: mean -1.19 versus -1.26 on control; difference 0.07 (95% CI -0.12 to 0.26), standardized effect d = 0.07; z-test p = 0.478.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 100 U/mL - Insulin Degludec and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in HbA1c at Week 52 in Participants Not Using GLP-1 Receptor Agonists [Noninferiority Analysis]

• 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:
  • 100 U/mL - Insulin Degludec: mean -1.15 versus -1.26 on control; difference 0.11 (95% CI -0.07 to 0.29), standardized effect d = 0.11; z-test p = 0.219.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 100 U/mL - Insulin Degludec and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in HbA1c at Week 52 [Superiority Analysis]

• 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:
  • 100 U/mL - Insulin Degludec: mean -1.17 versus -1.26 on control; difference 0.09 (95% CI -0.04 to 0.22), standardized effect d = 0.09; z-test p = 0.177.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 100 U/mL - Insulin Degludec and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary outcomes covering HbA1c in participants using and not using GLP-1 receptor agonists, HbA1c superiority analyses, time in a specified blood-glucose range, fasting blood glucose, and glucose variability. It lists 18 secondary outcomes and reports 18 secondary outcomes as posted. The measures broaden the assessment beyond the primary Week 52 noninferiority question, but they do not all address the same clinical or statistical question.

The available HbA1c subgroup analyses use the same general adjusted-means framework as the primary outcome. Their subgroup estimates are not, by themselves, evidence that treatment effects differ between subgroup categories. That claim would require a direct assessment of interaction or heterogeneity; such an analysis is not reported in the registry record. The HbA1c superiority result is also a distinct test from the primary noninferiority analysis. The remaining listed outcomes address glucose patterns and variability, but their numerical results are not included in the registry record for this analysis, so their direction and precision are not reported.

Secondary results can add context to the primary finding, but they carry less weight when many outcomes or subgroup analyses are examined without a clearly reported multiplicity strategy. Testing many hypotheses increases the chance of at least one apparently notable result occurring by chance. The registry record does not report whether or how multiplicity was controlled across secondary analyses. Consequently, secondary findings should be treated as supportive or exploratory unless the prespecified testing hierarchy and adjustment approach are available.

The secondary outcomes should not be used to fill the gap left by the unreported noninferiority margin. They describe other endpoints and populations; they do not establish the primary decision rule. Interpreting them alongside the primary result requires attention to their separate estimands, analysis populations, uncertainty, and multiplicity context.

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

• Change From Baseline in HbA1c at Week 52 in Participants Using GLP-1 Receptor Agonists [Noninferiority Analysis]
• Change From Baseline in HbA1c at Week 52 in Participants Not Using GLP-1 Receptor Agonists [Noninferiority Analysis]
• Change From Baseline in HbA1c at Week 52 [Superiority Analysis]
• Percentage of Time in the Blood Glucose Range Between 70 and 180 mg/dL [3.9 and 10.0 mmol/L] - Week 48 to Week 52
• Change From Baseline in HbA1c at Week 26 [Superiority Analysis]
• Percentage of Time in the Blood Glucose Range Between 70 and 180 mg/dL [3.9 and 10.0 mmol/L] - Week 22 to Week 26
• Change From Baseline in Fasting Blood Glucose (FBG)
• Glucose Variability

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: change in HbA1c is summarized as a mean for each treatment group. For a continuous outcome, a group mean gives a compact description of the central estimate, while a standard error describes the uncertainty around that estimated mean. The registry reports least-squares means and standard errors rather than unadjusted means and standard deviations.

What does ANCOVA contribute?

ANCOVA combines a comparison of treatment groups with adjustment for specified covariates. In general, adjustment can account for measured baseline or stratification factors and may improve precision when those variables are related to the outcome. The registry describes an ANCOVA model including baseline, country, GLP-1 receptor agonist use at randomization, sulfonylurea use at randomization, and treatment, using Type III sums of squares. The complete model specification, including any additional implementation details, is not reported in the registry record.

A least-squares mean is an estimate from the fitted model, adjusted for the variables included in that model. It is not necessarily identical to the arithmetic mean of the observed measurements. The reported LS mean difference compares the adjusted estimates. Its sign depends on the order used to define the contrast: the sponsor’s reported contrast is -0.09, while the simple recalculation is stated as degludec minus efsitora alfa and is 0.09. These are opposite orientations of the comparison.

How is noninferiority different from superiority?

In general, a superiority analysis asks whether evidence supports a difference favoring one treatment. A noninferiority analysis instead evaluates whether a treatment is not unacceptably worse than its comparator, using a prespecified margin. The margin defines the largest difference that would still satisfy the criterion. It is not reported in the registry record, and the primary sponsor-reported analysis has no p-value posted. Therefore, the estimates and confidence interval can be described, but the formal noninferiority decision cannot be reconstructed from the registry record alone.

The registry also lists a superiority analysis for the Week 52 HbA1c outcome. That is a separate question from the primary noninferiority analysis. Its reported p-value is 0.188, and its ANCOVA estimate and confidence interval are posted with that analysis. A statistical test result does not measure the size or clinical importance of an effect by itself; it should be considered alongside the estimate, uncertainty, analysis plan, and multiplicity context.

What does the recalculation represent?

The recalculated comparison uses posted summary statistics and is unadjusted. It is not the same as refitting the sponsor’s ANCOVA model with individual participant data. Its pooled standard deviation is marked as approximate, and the recalculated confidence interval and p-value should be understood as summary-statistic estimates. They provide a check on the scale and uncertainty of the contrast, not a replacement for the reported analysis.

The sponsor’s analysis includes adjustment variables and the stated missing-data procedure. Those features mean the sponsor estimate and the summary-statistic recalculation need not match exactly. In this record the estimates have opposite signs because the contrasts are oriented differently, while the confidence intervals express the corresponding ranges in those respective directions.

How are missing Week 52 outcomes handled?

The registry says that missing Week 52 data were imputed using a return-to-baseline multiple-imputations approach. In general, multiple imputation represents uncertainty about missing values by creating multiple completed datasets, analyzing each dataset, and combining the results. A return-to-baseline approach uses an assumption that missing outcomes move toward baseline rather than simply carrying forward the last observed value. The exact implementation details and sensitivity analyses are not reported in the registry record, so the assumptions cannot be fully evaluated from the posted description.

The primary population is defined as randomized participants who received at least one dose and had an HbA1c measurement at baseline or Week 52, excluding participants who discontinued study drug because of inadvertent enrollment. This is the population description attached to the endpoint analysis; it should not be conflated with the enrollment figure for the overall trial.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is an LS mean difference of -0.09, with a 95% confidence interval from -0.22 to 0.04. The interval communicates the uncertainty around the estimated contrast under the reported analysis. In general, a confidence interval gives a range of values compatible with the data and statistical model at its stated confidence level; it is not a guarantee that the true value lies within the interval.

The interval includes zero, so the posted primary estimate does not establish a difference in either direction under a conventional test of a zero contrast. But the primary analysis was specified as noninferiority, and a zero-difference test is not the same as evaluating a noninferiority margin. Since that margin is not reported in the registry record, the interval cannot be used to verify whether the formal noninferiority criterion was met.

The unadjusted recalculation is 0.09, with a 95% confidence interval from -0.041 to 0.221, when the contrast is defined as degludec minus efsitora alfa. It also includes zero. Its endpoint and general direction correspond to the sponsor contrast after reversing the sign, but the recalculation is based on summary statistics and is not the sponsor’s adjusted model. Its precision should therefore not be treated as an independent replication of the sponsor analysis.

Confidence intervals are more informative than a point estimate alone because they show the range of effects that remain consistent with the analysis. The intervals still permit effects on either side of zero. They should be interpreted in the scale of HbA1c change and in light of the missing noninferiority margin, the modeling approach, and the handling of missing data.

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: the primary outcome is continuous, and the sample-size assumptions specify participants per arm. In general, 80% power describes the chance of detecting the chosen effect under the stated assumptions when that effect is present; the 90% column uses a higher target chance of detection and therefore calls for a larger planning sample under otherwise comparable assumptions.

The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. Its rows therefore represent planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects need more participants to detect with the same target power, which is why the planning requirements rise as the assumed effect becomes smaller.

These are illustrations computed from the observed effect, not the trial’s original design calculations. They are not observed power. The trial’s own sample-size justification and original design assumptions are not reported in the registry record. The planning curve should be read as showing how the illustrative participant requirement changes with the effect being targeted, under the stated assumptions, rather than as a reconstruction of the trial’s design or a measure of what the completed study achieved.

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 = 0.090; pooled standard deviation σ = 1.012.
2. n = 2 × (1.96 + 0.842)² × 1.012² / 0.090² = 1,984.0, rounded up to 1,984 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 <- 0.0900000000000001                      # observed difference in means
sigma <- 1.01178936008633                     # 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(5362058)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,984 (80% power), 2,656 (90% power)
 75% of observed effect: n per arm = 3,528 (80% power), 4,722 (90% power)
 50% of observed effect: n per arm = 7,936 (80% power), 10,624 (90% power)
power.t.test: 1984.9 
Simulated power at n = 1,984 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor-reported primary analysis used ANCOVA and expressed the LS mean difference as -0.09, with a 95% confidence interval from -0.22 to 0.04. The registry record does not post a p-value for this primary noninferiority analysis. The summary-statistic recalculation expresses the contrast in the reverse order, degludec minus efsitora alfa, and gives 0.09 with a 95% confidence interval from -0.041 to 0.221.

The opposite signs reflect contrast orientation: reversing which group is subtracted from which changes the sign. The estimates are also from different procedures. The sponsor analysis adjusts for the covariates stated in the ANCOVA description and uses the stated missing-data imputation approach. The recalculation is an unadjusted approximation from posted summary statistics. It should be viewed as a secondary check, not as a replacement for the sponsor’s analysis.

The registry record does not flag a discrepancy between the posted summary and reported analysis. The noninferiority margin is not reported in the registry record, so neither the recalculation nor the posted sponsor interval alone permits an independent check of the formal noninferiority criterion.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, subgroups, or time points are tested. In general, the more statistical tests performed, the greater the chance that at least one result may appear unusual by chance alone. Methods such as a prespecified testing hierarchy or adjustment of significance thresholds can address this issue, but the registry record does not report a multiplicity procedure for the secondary analyses.

The record identifies a primary noninferiority endpoint and lists secondary outcomes, including subgroup-specific HbA1c analyses and a superiority analysis. It does not report the full testing hierarchy, whether secondary tests were confirmatory or exploratory, or whether any adjustment was used. The reported secondary p-value should therefore be read as the result of its stated analysis, not as evidence that the broader set of outcomes was controlled for multiplicity.

Missing Week 52 HbA1c values were handled using return-to-baseline multiple imputation, according to the primary endpoint description. In general, imputation makes assumptions about unobserved outcomes, and different assumptions can affect an estimate. The registry description does not provide complete implementation details or report sensitivity analyses that show how conclusions respond to alternative missing-data assumptions. Those details are not reported in the registry record.

The primary analysis population includes randomized participants who received at least one dose and had HbA1c measured at baseline or Week 52, with participants discontinuing study drug because of inadvertent enrollment excluded. This definition differs from a statement that every randomized participant contributed a Week 52 observation. The registry record does not provide enough information to determine how all departures from treatment, missing measurements, or other protocol deviations were handled beyond the stated imputation and population description.

The original sample-size justification, the planned noninferiority margin, interim analyses, and a complete statistical analysis plan are not reported in the registry record. Without these elements, readers cannot fully reconstruct the planned decision process or assess whether all analyses were conducted as prespecified.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypoglycaemia (1.1%), osteoarthritis (0.9%), arteriosclerosis coronary artery (0.6%), gastrooesophageal reflux disease (0.6%), abnormal uterine bleeding (0.5%).

The registry lists serious adverse events for participants at risk in each group. For insulin efsitora alfa, 41 affected participants are listed among 466 at risk; for insulin degludec, 38 affected participants are listed among 462 at risk. These figures describe the registry’s serious-adverse-event counts and at-risk groups. They should not be treated as a complete account of event severity, timing, recurrence, or causal relationship to treatment.

The most frequently listed serious-event terms include hypoglycaemia at 1.1%, osteoarthritis at 0.9%, arteriosclerosis coronary artery at 0.6%, gastrooesophageal reflux disease at 0.6%, abnormal uterine bleeding at 0.5%, and endometrial hyperplasia at 0.5%. The record also lists deaths: 2 in the efsitora alfa group and 1 in the degludec group. These figures are descriptive; the registry record does not establish that a listed event or death was caused by a study treatment.

For other adverse events, the record lists 195 affected participants among 466 at risk in the efsitora alfa group and 224 among 462 at risk in the degludec group. Differences in these counts alone do not determine comparative safety. Interpretation would require context such as event definitions, exposure, severity, timing, and the statistical approach, which is not fully reported in the registry record.

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

The posted results describe a randomized comparison of once-weekly insulin efsitora alfa and once-daily insulin degludec in adults with type 2 diabetes starting basal insulin for the first time. The primary outcome was change in HbA1c from baseline to Week 52. The sponsor-reported adjusted estimate was -0.09, with a 95% confidence interval from -0.22 to 0.04, for the stated contrast. The summary-statistic recalculation uses the reverse contrast and gives 0.09, with a 95% confidence interval from -0.041 to 0.221.

These estimates describe the size and uncertainty of the group comparison under their respective analyses. They do not, on their own, establish that either treatment is better, equivalent, or noninferior. A formal noninferiority conclusion depends on the prespecified margin, which is not reported in the registry record. The primary sponsor analysis also does not have a posted p-value, and the recalculation is not a substitute for that adjusted analysis.

The results apply to the study population and the stated analysis conditions. They should not automatically be generalized to people who were not represented by the trial’s eligibility criteria or treatment context. The study was open-label, and the endpoint was analyzed at Week 52; the record does not report all details needed to assess possible effects of awareness of treatment assignment or the robustness of findings under alternative analytic assumptions.

Safety counts are descriptive and do not by themselves establish cause or comparative risk. Secondary outcomes may add context, but multiplicity procedures are not reported, and the subgroup findings do not establish treatment-effect differences between subgroups. Overall, the posted information supports a careful description of the estimates and their uncertainty, while leaving important elements of the formal noninferiority decision and analysis plan unavailable in the registry record.

18. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to interpret a noninferiority comparison when the numerical contrast is available but the margin is not. The point estimate and confidence interval describe the observed comparison, yet the noninferiority margin defines what difference would count as an acceptable loss. Without that threshold, readers can inspect the estimate and uncertainty but cannot independently verify the formal noninferiority criterion.

The record also illustrates why contrast direction matters. The sponsor reports an LS mean difference of -0.09, while the recalculation reports 0.09 because it subtracts the groups in the opposite order. Both statements can describe the same underlying comparison when their directions are made explicit. Reporting the group order alongside an estimate helps prevent an apparent sign conflict from being mistaken for a disagreement in the data.

There is also a distinction between an adjusted sponsor analysis and a summary-statistic recalculation. The former uses the stated ANCOVA covariates and missing-data approach; the latter is an unadjusted approximation. Looking at both can aid interpretation, but they answer the question through different procedures and should not be treated as interchangeable.

Finally, the trial combines a primary endpoint with multiple secondary measures and subgroup analyses. This makes clear why the analysis hierarchy and multiplicity approach matter: an isolated secondary result should not carry the same evidential weight as a prespecified primary comparison unless the broader testing strategy is understood. The registry record gives enough information to describe several key statistical features, while leaving the margin and some planning and analysis details unreported.

19. Limitations

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

Several trial-specific limitations affect interpretation. The registry describes the study as open-label, so participants and study personnel knew the assigned treatment. Awareness may influence behavior, reporting, or care processes, although the record does not establish whether it did so in this study. The primary outcome is a laboratory measure, but the open-label design remains relevant to other aspects of conduct and to secondary outcomes that may depend on participant behavior or monitoring.

The noninferiority margin is not reported in the registry record. This is a central limitation for independently assessing the primary objective, because noninferiority is defined relative to that margin. The primary sponsor-reported analysis also has no posted p-value. The available confidence interval provides useful information about uncertainty but cannot substitute for the missing decision threshold.

The primary analysis uses a stated ANCOVA model and a return-to-baseline multiple-imputation approach for missing Week 52 data. The full implementation details and sensitivity analyses are not reported in the registry record. As a result, readers cannot assess how robust the estimate is to alternative missing-data assumptions or reproduce the complete analysis from the information described.

The simple recalculation is approximate and unadjusted, so it is not a direct replication of the sponsor’s model. Secondary endpoints and subgroup analyses raise multiplicity concerns, but the record does not report a complete adjustment strategy or testing hierarchy. The original sample-size justification, interim analyses, and complete statistical analysis plan are also not reported in the registry record. These gaps limit independent evaluation of prespecification and the strength of conclusions beyond the posted estimates.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Insulin Efsitora Alfa (LY3209590) Compared to Degludec in Adults With Type 2 Diabetes Who Are Starting Basal Insulin for the First Time — NCT05362058.
• Registry record last updated 2025-05-16; status last verified 2025-05.
• Results first posted 2025-05-16.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT05362058 is a completed Phase 3, randomized, open-label, parallel-design comparison of insulin efsitora alfa and insulin degludec in adults with type 2 diabetes starting basal insulin for the first time. The study lists enrollment of 928. Efsitora alfa was administered once weekly and degludec once daily during a 52-week treatment period, followed by a 5-week safety follow-up.

The primary endpoint was change from baseline in HbA1c at Week 52, assessed for noninferiority using ANCOVA. The sponsor-reported LS mean difference was -0.09, with a 95% confidence interval from -0.22 to 0.04. A summary-statistic recalculation in the reverse contrast direction was 0.09, with a 95% confidence interval from -0.041 to 0.221. The noninferiority margin is not reported in the registry record, so the formal criterion cannot be independently checked from the available description.

The record includes secondary outcomes and adverse-event counts, but multiplicity handling and several details of the original statistical plan are not reported in the registry record.