A Study of LY900014 in Participants With Type 1 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of LY900014 in Participants With Type 1 Diabetes (NCT03214367), 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 trial asked whether LY900014, given shortly before meals alongside basal insulin, differed from insulin lispro on change in HbA1c by Week 26 in adults with type 1 diabetes. It also included an open-label group given LY900014 after meals. The registry describes the study’s main purpose as evaluating LY900014 compared with insulin lispro, with either treatment used alongside insulin glargine or insulin degludec.

HbA1c is a measure related to average plasma glucose over a prolonged period. The main statistical question is about the estimated group-level change and its uncertainty, not whether an individual participant’s glucose control changed in a particular way. The record also lists postprandial glucose, hypoglycemia, insulin dose, and treatment satisfaction among secondary outcomes; these address other aspects of the study but do not replace the prespecified primary endpoint.

3. Trial Design

This was a Phase 3, randomized, parallel-group study with double masking for the main comparison. Its official title also identifies an open-label postprandial LY900014 treatment group, so masking was not uniform across every group. The registry lists an enrollment of 1392 and the study status as completed. The record gives a start date of 2017-07-17 and a primary completion date of 2018-09-06.

The principal meal-time regimens were LY900014 or insulin lispro given 0-2 minutes before meals. Both were paired with basal insulin glargine, given once or twice daily, or insulin degludec, given once daily. The additional open-label regimen used LY900014 20 minutes after the start of each meal. Prandial insulin doses were individualized and titrated according to protocol-defined targets. These features mean the comparison concerns treatment strategies implemented with basal insulin, rather than a meal-time drug considered independently of the rest of the regimen.

The primary outcome was change from baseline in HbA1c at Week 26 under an efficacy estimand. Its analysis population required baseline and at least one post-baseline HbA1c measurement. The registry states that outcome measures were reported for the main global study groups and not for the Maximum Extended Enrollment groups. Arm counts for the primary endpoint are 428 for LY900014, 309 for LY900014 Postmeal, and 417 for insulin lispro. These are endpoint analysis counts, not a replacement for the registry’s overall enrollment figure.

The registry describes the primary model as mixed model repeated measures, with treatment and specified stratification factors as fixed effects and baseline as a covariate. It also reports separate mixed-model comparisons classified as non-inferiority analyses. The original sample-size rationale, the non-inferiority margin, and any planned interim analyses are not reported in the registry record. Those omissions limit what can be said about the design’s operating assumptions.

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 either LY900014 at mealtime, Insulin Lispro (Humalog) at mealtime, or LY900014 administered 20 minutes after the start of a meal (LY900014 Postmeal) in the treatment period (Period 2).

Only the first 6 of 8 groups are shown.

Lead-in Period

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 one 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.

Only the first 6 of 7 groups are shown.

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, reported as a least-squares mean. The registry defines HbA1c as the glycosylated fraction of hemoglobin A and notes that it is measured to identify average plasma glucose concentration over prolonged periods. A change score describes how the measured value at follow-up differs from the participant’s baseline value; the group estimate summarizes that change for the analysis population.

HbA1c is used because it reflects glucose exposure over a prolonged period rather than a single reading. That makes it relevant to a trial comparing meal-time insulin regimens over the study period. It does not, by itself, describe day-to-day glucose variation or every event that may matter to participants. The registry therefore includes other outcomes, such as postprandial glucose excursions and hypoglycemia, alongside the primary measure.

The primary result is expressed as a least-squares mean from a mixed model repeated measures analysis. In general, a model-based mean can account for specified covariates and design factors, rather than being only a raw average of the observed values. The registry says that treatment and strata for pooled country, type of basal insulin, prandial insulin dosing plan, and HbA1c stratum were included as fixed effects, with baseline as a covariate. The efficacy estimand included data before permanent discontinuation of study drug when the baseline and post-baseline measurement requirements were met.

The reported standard errors describe the estimated precision of the group means, not the spread of individual participant outcomes. The registry does not state the numerical non-inferiority margin. Therefore, the endpoint estimates can be described, but a margin-based conclusion cannot be independently reconstructed from the record alone.

7. Results Posted in the Registry

• LY900014 Postmeal: mean 0.08 versus -0.13 on control; difference 0.21 (95% CI 0.12 to 0.30), standardized effect d = 0.33; z-test p = <0.001.
• Insulin Lispro (Humalog): mean -0.05 versus -0.13 on control; difference 0.08 (95% CI -0.01 to 0.17), standardized effect d = 0.13; z-test p = 0.068.

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 1-hour Postprandial Glucose (PPG) Excursion During Mixed-Meal Tolerance Test (MMTT) Efficacy Estimand at Week 26

• 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 Postmeal: mean 12.50 versus -28.60 on control; difference 41.10 (95% CI 31.29 to 50.91), standardized effect d = 0.63; z-test p = <0.001.
  • Insulin Lispro (Humalog): mean -0.70 versus -28.60 on control; difference 27.90 (95% CI 18.66 to 37.14), standardized effect d = 0.42; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for LY900014 Postmeal than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Insulin Lispro (Humalog) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in 2-hour PPG Excursion During MMTT Efficacy Estimand at Week 26

• 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 Postmeal: mean -10.20 versus -34.70 on control; difference 24.50 (95% CI 11.26 to 37.74), standardized effect d = 0.28; z-test p = <0.001.
  • Insulin Lispro (Humalog): mean -3.50 versus -34.70 on control; difference 31.20 (95% CI 18.71 to 43.69), standardized effect d = 0.35; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for LY900014 Postmeal than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Insulin Lispro (Humalog) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Rate of Severe Hypoglycemia at Week 26

• 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 Postmeal: 13.70 versus 16.50 (Events per 100 participant years) on control; rate ratio 0.83 (95% CI 0.49–1.40, approximate, Poisson model); p ≈ 0.487.
  • Insulin Lispro (Humalog): 18.34 versus 16.50 (Events per 100 participant years) on control; rate ratio 1.11 (95% CI 0.71–1.74, approximate, Poisson model); p ≈ 0.642.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between LY900014 Postmeal and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Insulin Lispro (Humalog) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoints cover several domains rather than a single repeated measure of the primary question. These include postprandial glucose excursions during a mixed-meal tolerance test, severe and documented symptomatic hypoglycemia, 1,5-AG, self-monitoring blood glucose, insulin dose, and treatment satisfaction. The posted detailed results include continuous postprandial glucose outcomes and severe hypoglycemia rates. The registry record lists additional secondary outcomes, but their numerical results are not reported in the registry record in the information available for interpretation.

Overall, the posted secondary findings are not uniform across outcomes or treatment comparisons. The registry’s reported analyses include model-based comparisons for postprandial glucose and event rates for severe hypoglycemia. These outcomes differ from HbA1c in their clinical content, measurement scale, and statistical model. Their pattern can provide context for the primary endpoint, but they do not provide a single confirmation or contradiction of it.

Secondary outcomes often involve multiple comparisons. In general, testing many endpoints and contrasts increases the chance that some results appear noteworthy by chance if no adjustment or hierarchy is used. The multiplicity strategy is not reported in the registry record. Accordingly, unadjusted secondary p-values carry less weight than a result from a clearly prespecified primary analysis with a stated decision rule. A small p-value in one secondary comparison should not be treated as proof that all related outcomes support the same conclusion.

The primary HbA1c endpoint and the secondary outcomes answer complementary questions. HbA1c represents a longer-term glycemic measure, while postprandial glucose describes meal-related excursions and hypoglycemia outcomes describe safety events. Differences between outcomes can reflect their different definitions, follow-up, and data distributions; they should not be compressed into an overall claim of benefit or harm without a prespecified framework.

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

• Change From Baseline in 1-hour Postprandial Glucose (PPG) Excursion During Mixed-Meal Tolerance Test (MMTT) Efficacy Estimand at Week 26
• Change From Baseline in 2-hour PPG Excursion During MMTT Efficacy Estimand at Week 26
• Rate of Severe Hypoglycemia at Week 26
• Rate of Documented Symptomatic Hypoglycemia at Week 26
• 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 analysis uses a mixed model repeated measures approach and reports least-squares means. The model description names treatment and the listed strata as fixed effects, with baseline HbA1c as a covariate. In general, a repeated-measures model can use observations collected at multiple study visits while accounting for their correlation within a participant. A covariate-adjusted estimate can differ from a simple difference between posted group means because it incorporates model terms and the available repeated measurements.

What does a least-squares mean represent?

In general, a least-squares mean is a model-based estimate of a group mean after accounting for specified factors in the model. It is not necessarily identical to the arithmetic average of the observed values. Here, the registry names treatment, strata, and baseline as model components. It does not give the complete model specification, covariance structure, or all implementation details in the record. The posted estimates should therefore be interpreted as the sponsor’s model-adjusted results, rather than as values that can be fully recreated from the summary statistics alone.

Why can a recalculation differ from the sponsor analysis?

The recalculated comparisons use posted arm-level means and standard errors to form simple unadjusted comparisons. They do not reproduce the sponsor’s mixed model, adjustment for strata and baseline, repeated-measures structure, or analysis estimand. The calculations are useful as a transparent check on the direction and approximate scale of the group summaries, but they do not supersede the analysis specified and reported by the sponsor. In this trial, the record flags a discrepancy, so the sponsor’s own analysis takes precedence.

There is also a sign-convention issue to keep in mind. A group difference changes sign when the order of subtraction is reversed. The primary reported values and the recalculated values use different apparent ordering. The associated confidence intervals and p-values also arise from different analyses, so the estimates should not be reconciled by changing signs alone.

What do standard errors and confidence intervals convey?

In general, a standard error measures the uncertainty in an estimated mean, while a confidence interval describes a range of values compatible with the data and analysis at a stated confidence level. Neither is the range of individual participant outcomes. A narrow interval indicates greater precision for the estimate; a wide interval indicates more uncertainty. The registry reports standard errors for the primary arm means and gives 95% confidence intervals for the sponsor’s comparisons.

For the recalculated mean comparisons, intervals are derived from posted summary statistics and should be regarded as approximate and unadjusted. The registry’s sponsor analyses use model-based least-squares mean differences. The two kinds of intervals answer related but not identical questions. A confidence interval crossing zero in an ordinary difference analysis indicates that the data are compatible with values on either side of zero under that calculation; it does not by itself settle the sponsor’s non-inferiority question. For non-inferiority, the interval must be assessed against the prespecified margin, which is not reported in the registry record.

Why do event rates need a different treatment?

The severe hypoglycemia outcome is expressed as events per 100 participant years, rather than as a continuous mean. The recalculation uses a Poisson rate approach. In general, count data may show over-dispersion when their variability exceeds what a basic Poisson model assumes. In that situation, a simple Poisson-based interval or test can understate uncertainty if the model does not allow for the extra variation. The registry record does not provide a sponsor analysis for these rate comparisons, and the recalculated p-values are unadjusted.

Rates also depend on time at risk, not only the number of participants. The registry lists rates and the number at risk for each group, but a full reconstruction of participant-time and event handling is not possible from the posted summary alone. The rate comparison should therefore be read as a descriptive, unadjusted statistical comparison, not as a substitute for a detailed event-level model.

What does the estimand and analysis population specify?

An estimand defines the treatment effect being targeted, including how events such as treatment discontinuation are handled. The registry calls the primary target an efficacy estimand and states that participant data were included when baseline and at least one post-baseline measurement were available before permanent study-drug discontinuation. This description indicates that post-discontinuation measurements were not included in that estimand. The record does not provide enough detail to determine how every intercurrent event or missing measurement was handled in the model.

The primary population also has a measurement requirement: randomized participants needed baseline and at least one post-baseline HbA1c value. In general, analyzing participants with observed follow-up data can create uncertainty if missingness is related to outcome or treatment. The model and estimand may address some aspects of the data structure, but the registry record does not report a full missing-data sensitivity analysis. The analysis population should not be confused with everyone randomized or with the overall enrollment figure.

11. Confidence Intervals and Precision

Precision is about how narrowly the estimate is determined by the data and analysis. For the sponsor’s primary LY900014-versus-insulin-lispro comparison, the reported least-squares mean difference is -0.08, and its 95% confidence interval runs from -0.16 to 0.00. For LY900014 Postmeal versus insulin lispro, the estimate is 0.13, with a 95% confidence interval from 0.04 to 0.22. These intervals communicate uncertainty around model-based group differences; they do not show the range of individual HbA1c changes.

The unadjusted recalculated interval for LY900014 versus insulin lispro runs from -0.006 to 0.166, while the interval for LY900014 Postmeal versus insulin lispro runs from 0.118 to 0.302. These recalculated intervals are based on posted summary statistics and are not the sponsor’s adjusted analysis. They should be kept distinct from the sponsor’s reported 95% intervals, especially because the record flags a discrepancy.

For an ordinary difference, an interval that includes zero indicates uncertainty about whether the difference is positive or negative under that analysis. An interval that excludes zero is evidence of a nonzero difference under its assumptions, but it does not establish that a difference is meaningful to patients. For non-inferiority, the key reference is the prespecified margin, not zero alone. That margin is not reported in the registry record.

Precision also depends on the endpoint and its scale. The primary endpoint is a model-based continuous measure, while severe hypoglycemia is a rate based on events and time at risk. Their estimates cannot be compared simply by looking at the numerical width of intervals. In general, event-rate estimates can be especially uncertain when event counts are limited or variability is greater than assumed by the model. The posted rate comparisons are unadjusted recalculations, so their uncertainty should be interpreted cautiously.

The standard errors listed for the primary arm means quantify uncertainty in those estimated means. They are not standard deviations and do not describe how much participants vary from one another. The registry does not provide the raw participant-level distribution needed to assess individual variability directly.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original sample-size design. For the continuous endpoints and the rate comparisons shown, the figures are participants per arm. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is the stated fraction of the observed effect. For time-to-event planning, the stated convention is total events using the Schoenfeld method; that is distinct from the participant-per-arm figures for the comparisons.

The 80% power column gives an illustrative number of participants per arm that, under the stated assumptions and effect size, would yield an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm under the same assumptions. These columns are design calculations, not observed characteristics of the trial.

Rows for planning at 100% of the observed effect use the full effect estimate as the target; rows at 75% and 50% use smaller target effects. Smaller effects are harder to distinguish from random variation and therefore require more participants. The figures are illustrative because they use the observed effect as an input, and the observed effect itself is uncertain. They should not be treated as a recommended design or as evidence that the completed trial had a particular probability of success. This is not observed power.

For a rate outcome, the assumptions behind a simple planning calculation may not capture variation in follow-up time, event clustering, or over-dispersion. The sample-size illustration is not a replacement for a prospective design based on the anticipated event rate, duration, analysis model, and clinically relevant target. The registry’s original sample-size justification and trial-specific planning assumptions are not reported in the registry record.

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 = 0.210; pooled standard deviation σ = 0.631.
2. n = 2 × (1.96 + 0.842)² × 0.631² / 0.210² = 141.5, rounded up to 142 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 <- 0.21                      # observed difference in means
sigma <- 0.630531808796957                     # 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(3214367)
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 = 142 (80% power), 190 (90% power)
 75% of observed effect: n per arm = 252 (80% power), 337 (90% power)
 50% of observed effect: n per arm = 567 (80% power), 758 (90% power)
power.t.test: 142.5 
Simulated power at n = 142 per arm: 0.806 (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’s own primary analyses are mixed-model comparisons of least-squares means and are labeled non-inferiority. They report a difference of -0.08 for LY900014 compared with insulin lispro, with a 95% confidence interval from -0.16 to 0.00 and p = 0.060. For LY900014 Postmeal compared with insulin lispro, the reported difference is 0.13, with a 95% confidence interval from 0.04 to 0.22 and p = 0.003.

The recalculations use only posted arm-level means and standard errors and are simple, unadjusted comparisons. Their estimates and p-values need not match the sponsor’s results because they do not recreate the model, covariate adjustment, repeated-measures structure, or estimand. The sign of a group difference also depends on subtraction order. In this record, the recalculated primary comparisons differ from the sponsor results, and that discrepancy is explicitly flagged. The sponsor’s own analysis takes precedence.

The sponsor’s reported label of non-inferiority does not by itself allow the reader to verify the decision. The margin and detailed decision rule are not reported in the registry record. The p-value for a difference from zero is not a substitute for checking whether an interval meets a non-inferiority criterion. The posted sponsor estimates are therefore the appropriate results to describe, while the available registry information does not support independently reconstructing the complete non-inferiority assessment.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, groups, time points, or contrasts are tested. In general, the more statistical tests conducted, the greater the chance that at least one result appears statistically notable by chance when all null hypotheses are true. Trial analysis plans often address this through a hierarchy of endpoints, adjusted significance thresholds, or other prespecified procedures. The multiplicity strategy for this trial is not reported in the registry record.

The primary endpoint is clearly identified as change from baseline in HbA1c at Week 26, and the sponsor reports two primary comparisons against insulin lispro. The registry labels these as non-inferiority analyses but does not report the non-inferiority margin. Without the margin and the full decision rule, readers cannot independently assess the non-inferiority criterion from the reported estimates and p-values alone. The record also does not report whether the comparisons were adjusted for multiplicity.

Several secondary outcomes and contrasts are listed. The registry supplies detailed numerical outcomes for some, but the multiplicity approach for interpreting these secondary tests is not reported in the registry record. The reported secondary p-values should therefore be read as nominal unless the complete analysis plan specifies otherwise. This qualification does not erase the estimates; it limits how strongly they can be treated as confirmatory evidence.

Missing data and analysis populations also affect interpretation. The primary efficacy estimand includes data before permanent discontinuation of study drug when baseline and at least one post-baseline HbA1c measurement are available. Thus, the endpoint population is not simply everyone randomized, and the registry explicitly says that the Maximum Extended Enrollment groups are not included in reported outcome measures. The record does not describe in full how missing values were modeled, what assumptions were made about why measurements were missing, or whether sensitivity analyses tested those assumptions.

In general, model-based analyses can use incomplete repeated measurements under assumptions about the missing-data process, but those assumptions cannot be confirmed from group summary statistics. A complete assessment would require the detailed statistical analysis plan and sensitivity analyses. Those details are not reported in the registry record, so uncertainty about missingness and multiplicity remains part of the interpretation.

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 (14.3%), diabetic ketoacidosis (6.5%), pyrexia (3.2%), appendicitis (3.2%), pyelonephritis acute (3.2%).

The registry reports serious adverse event counts and other adverse event counts for groups with stated numbers at risk, as well as deaths. These are descriptive summaries, not adjusted comparisons. For the main LY900014 group, the record lists 54 serious adverse events among 451 at risk, 163 other adverse events among 451 at risk, and 1 death. For the main insulin lispro group, it lists 67 serious adverse events among 442 at risk, 147 other adverse events among 442 at risk, and 1 death. The open-label LY900014 Postmeal group has 30 serious adverse events among 329 at risk, 104 other adverse events among 329 at risk, and 1 death.

The lead-in group is reported separately, with 48 serious adverse events and 131 other adverse events among 1316 at risk, and no deaths. The Maximum Extended Enrollment groups are also listed separately. Their results should not be combined with the main study arms without a justified analysis, particularly because the registry distinguishes those groups and states that primary outcome measures were not reported for them.

The serious-event terms listed include hypoglycaemia at 14.3%, diabetic ketoacidosis at 6.5%, pyrexia at 3.2%, appendicitis at 3.2%, pyelonephritis acute at 3.2%, and ligament rupture at 3.2%. The denominator and method for these percentages are not reported in the registry record. Counts alone do not show comparative risk, and these summaries do not establish that a treatment caused an event. The registry record does not provide an adjusted safety comparison in the information.

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

The primary endpoint describes modeled group-level change in HbA1c through Week 26 among participants meeting the registry’s efficacy-estimand measurement requirements. The sponsor reported model-based non-inferiority comparisons, while simple recalculations from posted group summaries produce different estimates. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence. The record does not state the non-inferiority margin, so an independent margin-based assessment is not possible from the registry record alone.

These results do not describe every participant’s response. A group mean can conceal substantial variation in individual outcomes, and the posted summaries do not provide participant-level distributions. Nor does HbA1c alone describe all aspects of glucose patterns or safety. The trial also measured postprandial glucose, hypoglycemia, and other outcomes, but those measures answer distinct questions and require their own interpretation.

The record describes a randomized study, which is an important design feature for comparing groups, but statistical interpretation still depends on the analysis population, estimand, missing-data handling, and prespecified decision rules. The primary population excludes participants without the stated measurement availability and the Maximum Extended Enrollment arms were not included in reported primary outcomes. The registry does not provide full missing-data sensitivity analyses or the multiplicity strategy.

In general, a p-value is not the probability that a treatment works, and a confidence interval is not a guarantee that the true effect lies within its limits. Estimates are conditional on the data, model, and assumptions used. The secondary findings and adverse event summaries can add context, but they should not be treated as a single overall treatment conclusion. This statistical reading does not establish clinical importance, causality for individual events, or conclusions beyond the outcomes and period reported in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why the reported estimand and analysis method matter. Its primary outcome is a model-adjusted change in HbA1c, and its sponsor analysis uses mixed models rather than a direct comparison of unadjusted arm means. Simple recalculations can help readers understand the scale of posted summaries, but they cannot recreate the sponsor’s model. When the calculations differ, as they do in this record, the sponsor analysis is the primary reference for the trial’s stated analysis.

The non-inferiority framing makes the decision rule especially important. A comparison with zero is not sufficient to establish non-inferiority; the estimate must be evaluated against a prespecified margin. Because that margin is not reported in the registry record, the statistical label can be reported, but the decision criterion cannot be independently checked. This is a practical example of why registry results are more interpretable when the margin and analysis plan are accessible.

The study also demonstrates that outcomes can point to different statistical questions. HbA1c, meal-related glucose excursions, and event rates use different measurement scales and models. Reading them together requires attention to endpoints, uncertainty, and multiplicity rather than simply counting nominally favorable p-values.

Finally, the planning illustrations show how required sample size depends on the effect assumed for planning. Smaller target effects require more participants under the stated assumptions. Such calculations are planning aids, not proof that a completed study was adequately powered for every outcome. The original design assumptions are not reported in the registry record, so the illustrations should not be used to infer the study’s original design rationale.

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 does not report the non-inferiority margin or the detailed decision rule, limiting independent assessment of the primary non-inferiority analyses. The full statistical analysis plan, original sample-size justification, and any interim analyses are also not reported in the registry record. These gaps make it difficult to determine how all endpoints, contrasts, and analysis choices were planned and interpreted.

The primary reported population required baseline and at least one post-baseline HbA1c measurement before permanent discontinuation of study drug. This is the stated efficacy estimand, but the record does not provide full details of the missing-data model or sensitivity analyses. The Maximum Extended Enrollment groups are excluded from reported outcome measures under the registry description. This limits the scope of the primary results and makes the endpoint analysis counts distinct from overall enrollment.

The postmeal LY900014 group was open-label, unlike the double-masked main comparison. That difference in masking is relevant when interpreting outcomes that may be affected by treatment awareness, behavior, or reporting. The registry also reports individualized prandial dosing and titration according to protocol-defined targets, so the results concern treatment regimens implemented with those procedures and basal insulin options.

The recalculated comparisons are simple, unadjusted estimates from summary statistics and do not reproduce the sponsor’s model. The registry flags a discrepancy for the primary endpoint; the sponsor’s own analysis takes precedence. Secondary results are subject to the unreported multiplicity strategy, and the severe hypoglycemia comparisons are unadjusted rate recalculations. Adverse event counts are descriptive, and the denominator for listed serious-event term percentages is not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of LY900014 in Participants With Type 1 Diabetes — NCT03214367.
• Registry record last updated 2020-05-01; status last verified 2019-09.
• Results first posted 2020-05-01.
• 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

The registry describes a completed Phase 3 randomized, parallel-group study of LY900014 compared with insulin lispro in adults with type 1 diabetes, with an additional open-label LY900014 postmeal group. The main meal-time treatments were combined with insulin glargine or insulin degludec. The primary endpoint was change from baseline in HbA1c at Week 26 under an efficacy estimand.

The sponsor reported mixed-model non-inferiority comparisons. Simple recalculations from posted arm summaries differ, and the registry flags that discrepancy; the sponsor’s own analysis takes precedence. The non-inferiority margin, multiplicity strategy, original sample-size justification, and full missing-data sensitivity analyses are not reported in the registry record. Secondary outcomes and adverse event summaries provide additional context but do not replace the primary analysis or establish conclusions beyond the outcomes reported.