A Study of LY900014 Compared to Insulin Lispro in Participants With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of LY900014 Compared to Insulin Lispro in Participants With Type 2 Diabetes (NCT03214380), a randomized phase 3 study. The primary outcome is Change From Baseline in Hemoglobin A1c (HbA1c) Efficacy Estimand at Week 26.

2. Clinical Question

The clinical question is comparative rather than a comparison with no treatment: both groups received mealtime insulin and basal insulin. The registry lists insulin glargine and insulin degludec as basal options. It also lists metformin and an SGLT2 inhibitor among the study interventions, but the record does not specify their use in each participant or arm.

The primary endpoint concerns the change from baseline through Week 26, not a single HbA1c measurement in isolation. The registry describes an efficacy estimand that uses data available before permanent discontinuation of study drug, subject to having baseline and at least one post-baseline HbA1c value. This defines which observations contribute to the primary analysis; it does not by itself describe every possible treatment experience after discontinuation.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group study comparing LY900014 with insulin lispro in adults with type 2 diabetes. The registry describes the study as completed and records an enrollment of 933. The study started on 2017-07-14, and primary completion was recorded as 2018-08-14.

The two main treatment groups received their assigned mealtime insulin subcutaneously with each meal. Each could be used with basal insulin glargine or degludec. The registry describes basal glargine as given once or twice daily and degludec as given once daily, with listed concentrations varying by basal product. Mealtime doses were individualized and titrated according to protocol-defined targets. The registry does not report the detailed titration rules in the record.

The primary outcome results are reported for the main global study groups, not the Maximum Extended Enrollment groups. The registry states that this exclusion was prespecified in the analysis plan. The main primary endpoint analysis includes 335 participants in the insulin lispro arm and 334 in the LY900014 arm with outcome results. Those endpoint counts are not the same as total enrollment: the primary analysis population was defined by the availability of baseline and post-baseline HbA1c measurements.

The registry record does not report the original sample-size justification, randomization ratio, allocation concealment details, the methods used to maintain blinding, or a full schedule of study visits. It also does not give the eligibility criteria beyond the description of adults with type 2 diabetes in the study title and summary. These details should not be inferred from the randomized, double-blind, parallel-group labels.

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: The purpose of the Lead-in Period was to titrate basal insulin prior to randomization. Participants were then randomized to receive Insulin lispro (Humalog) or LY900014 in the Treatment Period (Period 2).

Lead-in

Reasons for not completing this period:

Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants with baseline and at least 1 post-baseline HbA1c data. As pre-specified in the analysis plan, outcome measures will not be reported for the Maximum Extended Enrollment (MEE) arms/groups but only for the main global study arms/groups.

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 Hemoglobin A1c (HbA1c) Efficacy Estimand at Week 26, measured over Baseline, Week 26.

The primary endpoint is change from baseline in hemoglobin A1c (HbA1c) at Week 26, expressed as percentage of HbA1c. HbA1c is a continuous measure used to represent glycemia over time, rather than a reading taken at one moment. A change score compares the Week 26 value with the participant’s baseline value; the study’s reported group summaries are least-squares means, which are model-based estimates rather than simple arithmetic averages.

In a randomized comparison, this endpoint provides a way to assess the difference in average change between the assigned mealtime insulin groups while accounting for the analysis model’s specified terms. The registry describes the primary analysis as a mixed model for repeated measures (MMRM), including treatment, visit, treatment-by-visit interaction, strata, and baseline value. This allows repeated HbA1c measurements to contribute to the model rather than reducing the analysis to only one follow-up value.

The primary outcome population required a baseline HbA1c and at least one post-baseline measurement before permanent study-drug discontinuation. Thus, the endpoint is not a summary of every randomized participant regardless of measurement availability. The registry does not report further details about the clinical meaning of a particular magnitude of change, nor does the record state a non-inferiority margin. The endpoint estimates can therefore be described statistically, while conclusions that depend on an unreported threshold cannot be assessed from the registry record.

7. Results Posted in the Registry

• LY900014: mean -0.38 versus -0.43 on control; difference 0.05 (95% CI -0.07 to 0.17), standardized effect d = 0.07; z-test p = 0.400.

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.

1-hour Postprandial Glucose (PPG) Excursion During Mixed-Meal Tolerance Test (MMTT) Efficacy Estimand

• 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:
  • LY900014: mean 63.10 versus 74.90 on control; difference -11.80 (95% CI -21.78 to -1.82), standardized effect d = -0.19; z-test p = 0.020.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LY900014 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

2-hour PPG Excursion During MMTT Efficacy Estimand

• 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:
  • LY900014: mean 80.40 versus 97.80 on control; difference -17.40 (95% CI -29.87 to -4.93), standardized effect d = -0.22; z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LY900014 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Rate of Severe Hypoglycemia

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • LY900014: 2.44 versus 4.19 (Events per 100 participant years) on control; rate ratio 0.58 (95% CI 0.17–1.97, approximate, Poisson model); p ≈ 0.385.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between LY900014 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context beyond the primary HbA1c comparison, but they address different aspects of the study. The registry includes postprandial glucose excursions during a mixed-meal test, hypoglycemia outcomes, laboratory and self-monitoring measures, insulin dose, and treatment-satisfaction information. This breadth means the secondary findings should be understood as a collection of distinct questions, not as interchangeable measures of one treatment effect.

The two posted sponsor analyses for postprandial glucose are labeled superiority and report confidence intervals that lie below zero, while the severe hypoglycemia comparison is posted as a rate outcome with an unadjusted recalculation whose interval includes the rate-ratio reference value. These results do not change the interpretation of the primary HbA1c estimate: they concern separate outcomes, with different measurement scales and analysis methods. The registry record does not provide posted results for every named secondary outcome in the material.

Unadjusted secondary results carry less weight as a group when a multiplicity strategy is not reported. In general, examining many outcomes creates more opportunities for an apparently strong result to arise by chance, even if each test is considered on its own. The registry record does not report how multiplicity was handled across the secondary endpoints. Therefore, individual secondary p-values should be read as outcome-specific evidence rather than definitive confirmation across all secondary questions.

The different outcome types also bring different uncertainty. Continuous measures are summarized as mean differences, whereas severe hypoglycemia is expressed as events per participant time and compared with a rate ratio. The same numerical direction or p-value does not carry the same interpretation across those scales. A balanced reading considers the endpoint definitions, the sponsor’s reported analyses, the recalculations’ approximate nature, and the fact that these outcomes are secondary to the stated primary endpoint.

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

• 1-hour Postprandial Glucose (PPG) Excursion During Mixed-Meal Tolerance Test (MMTT) Efficacy Estimand
• 2-hour PPG Excursion During MMTT Efficacy Estimand
• Rate of Severe Hypoglycemia
• Rate of Documented Symptomatic Hypoglycemia
• Change From Baseline in 1,5-Anhydroglucitol (1,5-AG) at Week 26
• Change From Baseline in 10-Point Self-Monitoring Blood Glucose (SMBG) Values at Week 26
• Change From Baseline in Insulin Dose at Week 26
• Change From Baseline in Insulin Treatment Satisfaction Questionnaire (ITSQ) Regimen Inconvenience Domain Score at Week 26

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is analyzed using a mixed model for repeated measures (MMRM). In general, this type of model uses repeated outcome measurements from participants across visits and estimates treatment comparisons while accounting for the structure of those repeated observations. The registry says the model included fixed class effects for treatment, strata, visit, and treatment-by-visit interaction, as well as baseline value as a continuous fixed covariate. It identifies the strata as pooled country, type of basal insulin, and number of prandial doses at study entry. The registry does not report further model details, such as the covariance structure or the method used to handle missing observations.

The treatment-by-visit interaction allows the estimated treatment difference to vary by visit rather than requiring the same difference at every time point. The baseline covariate adjusts the outcome model for the recorded starting HbA1c value. In general, adjustment for baseline can improve precision when baseline is related to follow-up outcomes, but the result remains dependent on the specified model and available data. The primary endpoint is presented as a least-squares mean, meaning a model-based adjusted estimate for each group under the analysis model. The reported difference compares those adjusted estimates.

The primary efficacy estimand is described as including participant data when a baseline and at least one post-baseline HbA1c measurement were available before permanent study-drug discontinuation. In general, an estimand clarifies the treatment effect being targeted and how events such as treatment discontinuation are handled. This description sets a limit on which measurements contribute to the stated estimand. The registry does not report additional estimand strategies for observations after discontinuation, nor does it provide enough detail to reconstruct the full missing-data assumptions.

The recalculated continuous-outcome comparisons use posted group summaries to obtain an unadjusted comparison. They do not reproduce the covariate adjustment, repeated-measures structure, or estimand implementation of the sponsor’s MMRM. The recalculated pooled standard deviation is approximate because the posted arm summaries give standard errors, not participant-level standard deviations. In general, standard errors quantify uncertainty in estimated means, while standard deviations describe participant-to-participant variation. Recovering a pooled variation estimate from standard errors requires assumptions, so these recalculations are useful as a separate summary rather than a replacement for the sponsor’s model.

A confidence interval describes a range of values compatible with the data and analysis under the interval’s statistical assumptions. It reflects uncertainty in the estimated comparison; it is not a range containing a known fixed proportion of individual participant outcomes. For the simple recalculation, the interval is based on the posted summary values and is not the sponsor’s adjusted interval. For the sponsor analyses, the registry reports the adjusted interval directly. General interpretation should consider both the interval width and the location of the interval relative to the comparison value of zero for mean differences.

The two postprandial glucose outcomes have sponsor-reported ANCOVA analyses. In general, analysis of covariance (ANCOVA) estimates a group comparison while adjusting for specified covariates. The registry identifies the method and provides a net mean difference, confidence interval, and p-value for each of these two secondary outcomes. The record does not list all covariates used in those ANCOVA models, so their exact adjustment cannot be reconstructed from the stated method name alone.

Severe hypoglycemia is reported as a rate, in events per 100 participant years, rather than as a continuous mean or a simple proportion of participants. A rate uses event counts relative to time at risk. The recalculated comparison uses a Poisson approach and gives a rate ratio. In general, Poisson models are used for event counts over exposure time; they rely on assumptions about the count process. Over-dispersion occurs when the variability in counts exceeds what a basic Poisson model allows, and can make a simple Poisson-based uncertainty estimate too narrow. The registry does not report a sponsor analysis or modeling details for the severe hypoglycemia comparison.

The p-values attached to recalculated comparisons are unadjusted. In general, a p-value measures how inconsistent data are with a specified null hypothesis under a statistical model; it is not the probability that a treatment effect is absent or present. When many outcomes are examined, the chance of at least one apparently notable result can increase unless a multiplicity strategy is used. The registry record does not report an adjustment procedure across the secondary endpoints, so the separate secondary p-values should be interpreted cautiously rather than as a single confirmatory family of tests.

11. Confidence Intervals and Precision

The primary sponsor-reported comparison is 0.06, with a 95% confidence interval from -0.05 to 0.16. The interval spans values below and above zero, indicating uncertainty about the direction and size of the adjusted mean difference under the sponsor analysis. The registry labels this analysis non-inferiority, but does not report the margin needed to judge the interval against the non-inferiority criterion. Without that margin, the precision can be described numerically, but the decision threshold cannot be checked.

The unadjusted recalculation is 0.05, with a 95% confidence interval from -0.066 to 0.166. It is based on summary statistics and uses an approximate pooled standard deviation, so it should not be treated as an exact reconstruction of the MMRM. The closeness of its point estimate to the sponsor estimate does not make the analyses interchangeable: they differ in adjustment and calculation method.

In general, narrower confidence intervals indicate greater precision for the estimated comparison, while wider intervals leave more values compatible with the data. Precision is not the same as clinical importance. The registry does not provide a threshold for a clinically important HbA1c difference, and no such threshold should be inferred from the interval alone.

The secondary outcomes have their own intervals and scales. The sponsor-reported postprandial comparisons have intervals below zero; the severe hypoglycemia rate-ratio recalculation has an interval that extends on both sides of 1. These intervals should be interpreted according to their respective measures: zero is the reference for a mean difference, while 1 is the reference for a rate ratio. Differences in sample size, outcome variability, event frequency, and analysis method can all affect precision.

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 illustrations based on the observed effect, not the trial’s original design calculation. For the continuous outcomes, the figures mean participants per arm; for the event-rate illustration, the figures mean total events, using the Schoenfeld approach. The distinction matters: a per-arm participant target is not a total trial enrollment, and a total-event target is not a participant count.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set as a stated fraction of the observed effect. The registry record does not report the trial’s original sample-size justification, so these calculations should not be read as a description of the design decision made for this trial.

The 80% power column indicates the illustrated number of participants per arm, or total events for the rate outcome, under which a study would have an 80% chance of detecting the specified effect if the planning assumptions and effect were correct. The 90% power column uses a higher chance of detection and therefore requires a larger planning target under the same setup. These are prospective planning concepts, not properties measured after a trial has finished.

Each planning row uses a different fraction of the observed effect. A smaller assumed effect is harder to distinguish from random variation, so it requires more participants or events under the same assumptions. The calculations are sensitive to the observed effect used as their starting point; if that estimate is uncertain, the resulting planning targets are uncertain too. These figures are not observed power, and they do not establish whether the completed trial was adequately designed for its primary objective.

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 = 0.050; pooled standard deviation σ = 0.768.
2. n = 2 × (1.96 + 0.842)² × 0.768² / 0.050² = 3,705.0, rounded up to 3,706 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 <- 0.05                      # observed difference in means
sigma <- 0.768153189369692                     # 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(3214380)
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 = 3,706 (80% power), 4,961 (90% power)
 75% of observed effect: n per arm = 6,587 (80% power), 8,818 (90% power)
 50% of observed effect: n per arm = 14,821 (80% power), 19,841 (90% power)
power.t.test: 3706 
Simulated power at n = 3,706 per arm: 0.796 (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 gives a least-squares mean difference of 0.06 with a 95% confidence interval from -0.05 to 0.16 and labels the analysis non-inferiority. The registry describes the primary method as MMRM, with treatment, visit, treatment-by-visit interaction, strata, and baseline value included in the model. The reported analysis record does not name a method in its analysis-method field, but the primary endpoint description gives the MMRM specification.

The recalculation from posted arm summaries gives a mean difference of 0.05 and a 95% confidence interval from -0.066 to 0.166. This is an unadjusted, approximate calculation and does not replicate the sponsor’s repeated-measures model or its estimand. Its p-value of 0.4 is likewise an unadjusted recalculated result; the sponsor’s primary analysis record does not include a p-value.

The two estimates are close in their point values, but their methods and intervals are not identical. The sponsor’s confidence interval is the relevant reported interval for the sponsor analysis, while the recalculated interval is a separate descriptive check based on summary data. The registry does not state the non-inferiority margin, so the sponsor’s label cannot be independently evaluated against its criterion from the record alone. The record reports no discrepancy between the posted results and the recalculation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when an analysis evaluates several outcomes, time points, or comparisons. In general, as the number of statistical tests increases, the chance of obtaining at least one apparently notable result by chance can also increase. Methods such as prespecified testing sequences or adjusted significance thresholds can address this issue, but the registry record does not report a multiplicity strategy for the outcomes described.

The primary HbA1c endpoint is distinguished from secondary outcomes in the registry, and the primary description states that MEE groups are not reported for outcome measures under the prespecified analysis plan. However, the record does not specify a hierarchy among the secondary endpoints, whether particular secondary tests were confirmatory, or how conclusions were protected against multiple testing. The two sponsor-reported postprandial analyses and the unadjusted severe hypoglycemia recalculation should therefore be interpreted as individual outcome results, not as a unified familywise conclusion.

Missing data also affect interpretation. The primary efficacy estimand requires baseline and at least one post-baseline HbA1c measurement before permanent study-drug discontinuation. This definition indicates that participants without the required measurements do not contribute to that endpoint population as described. The endpoint counts are 335 for insulin lispro and 334 for LY900014, while total enrollment is 933; these figures refer to different populations and should not be treated as directly interchangeable.

The MMRM description gives the model terms but does not report its covariance structure or detailed assumptions about missing outcomes. The registry record also does not report sensitivity analyses assessing departures from those assumptions, the amount or pattern of missing data, or a full description of the analysis population beyond the stated inclusion criteria. Those omissions limit independent assessment of how robust the primary estimate is to missing-data choices.

The registry does state that the primary endpoint results are not reported for the MEE groups and gives this as a prespecified choice in the analysis plan. This helps define the scope of the posted primary results, but does not resolve the unreported multiplicity and missing-data details. Those are distinct design and analysis questions.

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 (1.5%), acute myocardial infarction (1.2%), sinusitis (1.2%), ligament sprain (1.2%), carpal tunnel syndrome (1.2%).

The registry reports serious adverse events and other adverse events by group, alongside the number of participants at risk. In the main insulin lispro group, 26 of 337 participants were listed as affected by serious adverse events; in the main LY900014 group, the corresponding count was 26 of 336. The record also lists other adverse events affecting 60 of 337 and 79 of 336, respectively. These are participant counts in the registry’s categories, not a comparison of event rates adjusted for follow-up time.

The registry records one death in the main insulin lispro group and two in the main LY900014 group. It separately lists lead-in and Maximum Extended Enrollment groups, which have different group sizes and should not be combined with the main treatment groups when reading these counts. The serious adverse-event terms reported most often include hypoglycaemia at 1.5%, followed by acute myocardial infarction, sinusitis, ligament sprain, carpal tunnel syndrome, and lumbar radiculopathy, each at 1.2%.

These descriptive counts do not establish that a difference between groups is statistically reliable or attributable to assigned treatment. The registry record does not provide a formal comparative safety analysis in the registry record, nor does it give detailed event definitions or adjudication procedures. The counts are best read as a summary of what was recorded, with the group denominators and separate enrollment categories kept in view.

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

The primary endpoint estimates the average model-based change in HbA1c through Week 26 for the specified efficacy estimand. The sponsor-reported comparison is a least-squares mean difference of 0.06, with a 95% confidence interval from -0.05 to 0.16. The unadjusted recalculation is close in point estimate but uses a different method and has its own interval. Together, these values describe the observed comparison and its uncertainty; they do not show that the groups are identical.

The registry labels the primary analysis non-inferiority. That label depends on comparing the relevant confidence interval with a prespecified non-inferiority margin. The margin is not reported in the registry record, so the statistical criterion underlying the label cannot be assessed from the posted information alone. The results should not be extended beyond the population, endpoint, and timeframe described in the record.

The secondary analyses concern additional measures, including postprandial glucose and hypoglycemia. They can provide complementary information, but they do not replace the primary endpoint or resolve its uncertainty. The registry record does not report a multiplicity approach across these outcomes, which limits the strength of conclusions based on separate secondary tests.

These statistical results are not individualized predictions. Group averages and confidence intervals do not describe every participant’s outcome, and they do not determine what will happen for a particular person. The trial record also does not establish the effects of using the listed treatments outside the study setting, nor does it report all details needed to assess generalizability. Interpretation is limited to the randomized comparison and outcomes recorded in this study.

Most importantly, statistical evidence is not a substitute for a clinical judgment about importance. The registry does not give a threshold for a clinically meaningful HbA1c difference, and statistical significance alone would not establish that an observed difference matters clinically. The available record supports a careful account of estimates, intervals, and analysis labels, while leaving some decision criteria and analysis details unreported.

18. Why This Trial Matters Statistically

This trial illustrates why a reported treatment comparison cannot be reduced to a single point estimate or p-value. The primary endpoint is a repeated-measures outcome analyzed with a specified model and an efficacy estimand. Its model-based sponsor result and the unadjusted recalculation are related summaries, but they answer the comparison using different methods. Keeping those methods distinct helps avoid treating an approximate reanalysis as though it were the sponsor’s prespecified analysis.

It also demonstrates the importance of the analysis criterion in non-inferiority studies. The registry labels the primary analysis non-inferiority, yet the margin is not reported in the record. A confidence interval alone does not define non-inferiority; its relation to the margin is central. The missing threshold therefore limits what can be independently concluded from the posted summary.

Secondary endpoints add breadth, but they also create interpretive complexity. Continuous postprandial outcomes and event rates have different scales and require different reference values. With no multiplicity strategy reported, each result needs to be interpreted in its own context, without treating isolated statistical signals as a coherent confirmatory conclusion.

Finally, the sample-size illustrations demonstrate how planning depends on an assumed target effect and analysis assumptions. They are not a retrospective measure of study success or a substitute for the trial’s original design justification, which is not reported in the registry record. Together, these features make the study useful for understanding the relationship between endpoint choice, model specification, uncertainty, missing information, and the strength of statistical claims.

19. Limitations

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

The registry record leaves several details unavailable for independent appraisal. The original sample-size justification, including the effect size and power target used during trial planning, is not reported. The planning illustrations based on observed effects should not be mistaken for those original design assumptions.

The primary analysis description identifies an MMRM and its listed terms, but does not give the covariance structure, detailed missing-data assumptions, or sensitivity analyses. The endpoint population is defined by baseline and post-baseline measurement availability before permanent discontinuation, but the amount and pattern of missing data are not reported in the record. These gaps limit assessment of the robustness of the primary estimate to model and missing-data choices.

The sponsor labels the primary result non-inferiority, but the non-inferiority margin is not reported. Without it, the criterion cannot be checked against the confidence interval. The registry also does not report a multiplicity strategy for the secondary endpoints, or fully specify the ANCOVA covariates for the postprandial analyses.

The simple recalculations use posted summary statistics rather than participant-level data. For continuous measures, the pooled standard deviation is approximate because the posted summaries provide standard errors. The rate comparison uses a Poisson approach, while the record does not include a sponsor analysis for that endpoint. These recalculations are therefore limited descriptive checks, not replacements for the trial’s full analysis.

Finally, the primary results exclude MEE groups according to the stated prespecified analysis approach, and the primary endpoint population is smaller than overall enrollment. Generalization beyond the analyzed population or the Week 26 timeframe is not established by these results alone. The registry record does not provide every detail needed to judge eligibility, adherence, or the full context of concomitant treatment use.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of LY900014 Compared to Insulin Lispro in Participants With Type 2 Diabetes — NCT03214380.
• Registry record last updated 2020-03-27; status last verified 2019-08-15.
• Results first posted 2020-03-27.
• 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

NCT03214380 is a completed, randomized, double-blind, parallel-group Phase 3 study comparing LY900014 with insulin lispro in adults with type 2 diabetes. The registry records 933 participants enrolled. Both mealtime insulin groups could receive basal insulin glargine or degludec, with individualized prandial dosing and protocol-defined titration.

The primary endpoint was change from baseline in HbA1c at Week 26. The sponsor-reported least-squares mean difference was 0.06, with a 95% confidence interval from -0.05 to 0.16, and the analysis was labeled non-inferiority. The non-inferiority margin is not reported in the registry record. An unadjusted recalculation gives a mean difference of 0.05, with a 95% confidence interval from -0.066 to 0.166.

Secondary outcomes cover postprandial glucose, hypoglycemia, and other measures. The registry record does not report a multiplicity strategy, and several analysis details are unavailable, including the original sample-size justification and key missing-data diagnostics. Interpretation should distinguish sponsor analyses from approximate recalculations and keep their uncertainty and limitations in view.