A Study of LY900014 and Insulin Lispro With an External Continuous Subcutaneous Insulin Infusion System in Adult Participants With Type 1 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of LY900014 and Insulin Lispro With an External Continuous Subcutaneous Insulin Infusion System in Adult Participants With Type 1 Diabetes (NCT03433677), a randomized phase 3 study. The primary outcome is Rate of Infusion Set Failures.

2. Clinical Question

The clinical question concerned compatibility and safety when LY900014 or insulin lispro was delivered through an external continuous subcutaneous insulin infusion system in adults with type 1 diabetes. The primary focus was the rate of infusion set failures during a 6-week treatment period. The registry defined a failure as a premature infusion set change associated with a pump occlusion alarm, or with unexplained hyperglycemia that remained above the specified threshold after a pump-delivered correction bolus.

The question is about a device-delivery outcome under the study conditions, not a broad comparison of all aspects of diabetes care. The registry also lists secondary outcomes relating to infusion set changes, insulin dosing, glucose response following correction boluses, and severe hypoglycemic events. The specific results for several of those outcomes are not reported in the registry record.

3. Trial Design

This was a phase 3, randomized, double-blind, crossover study sponsored by Eli Lilly and Company. Its official title describes a prospective comparison of LY900014 and insulin lispro with an external continuous subcutaneous insulin infusion system. The registry lists 49 participants as enrolled and the study as completed. The listed start date is 2018-02-21, and the primary completion date is 2018-09-04.

A crossover design generally compares treatments across periods within participants, which can reduce the influence of stable differences between individuals. That general feature does not establish the exact treatment sequence, period structure, or handling of period effects in this particular trial. Those details are not reported in the registry record. The registry identifies the design as crossover but does not report the treatment sequences or a washout procedure.

Both study treatments were delivered by individualized continuous subcutaneous insulin infusion. LY900014 and insulin lispro were each listed at a concentration of 100 U/mL. The registry describes the treatment period for the primary endpoint as 6 Weeks. It does not report the duration of every treatment period, any run-in period, or details of pump settings and adjustment procedures.

The primary analysis population is described as all randomized participants who received at least one dose of study drug. The arm results list 48 participants for insulin lispro and 49 for LY900014. These arm counts should not be interpreted as a count of independent people in a parallel-group trial: the study is identified as a crossover, and the registry does not explain how the treatment-period counts relate to the enrolled participant count.

The record identifies double masking, but does not specify which participant, investigator, or other roles were masked. Further detail on allocation procedures, the prespecified statistical plan, and the original sample-size justification is 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: 2-period crossover with no washout between periods and a 4 week safety follow-up.

Period 1

Reasons for not completing this period:

Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least 1 dose of study drug.

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 Rate of Infusion Set Failures, measured over 6 Weeks.

The primary endpoint was the rate of infusion set failures, expressed as events per 30 participant days over 6 Weeks. It counted events rather than simply recording whether each participant experienced any event. The registry definition includes premature infusion set changes due to a pump occlusion alarm, or due to unexplained hyperglycemia above 250 mg/dL (13.9 mmol/L) that did not decrease within 1 hour after a correction bolus delivered through the pump.

The rate was calculated for each participant using the total number of qualifying events and the participant’s exposure time on study treatment. The registry describes exposure as ending at the last dose, with pump or treatment interruptions excluded, and expresses the resulting rate on a 30-participant-day scale. This exposure-based measure is useful when participants contribute different amounts of treatment time: it relates the event count to time at risk rather than treating every participant as if they had identical exposure.

In general, an event rate can capture repeated failures that a simple participant-level indicator would not distinguish. It is therefore relevant to a compatibility question involving infusion set performance. It does not, by itself, describe the clinical consequences of each event or establish how the outcome would compare in other populations or delivery settings.

7. Results Posted in the Registry

• LY900014: 0.03 versus 0.05 (events per 30 participant days) on control; rate ratio 0.60 (95% CI 0.44–0.82, approximate, Poisson model); p ≈ 0.002.

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.

Percentage of Participants With at Least 1 Event of Infusion Set Failure

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • LY900014: 4.1% (2/49) versus 6.2% (3/48) on control; risk difference -2.2 percentage points (95% CI -11.0 to 6.6), risk ratio 0.65 (0.11–3.74); unadjusted two-proportion z-test p = 0.629.
• Interpretation:
  • The 95% confidence interval includes no difference, 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.

Rate of Premature Infusion Set Changes

• 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: 1.13 versus 0.78 (events per 30 participant days) on control; rate ratio 1.45 (95% CI 1.36–1.54, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for LY900014 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time Interval Until Infusion Set Change

• 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 74.30 versus 76.10 on control; difference -1.80 (95% CI -6.00 to 2.40), standardized effect d = -0.17; z-test p = 0.401.
• Interpretation:
  • The 95% confidence interval includes no difference, 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.

Across the posted secondary outcomes with numerical results, the pattern is mixed rather than uniformly pointing in one direction. The outcomes differ in what they measure: whether a participant experienced any failure, the rate of premature set changes, and the time interval until a set change. Each captures a separate aspect of infusion set performance, and none is a direct replacement for the primary endpoint’s defined failure rate.

The secondary results should be interpreted alongside, but not collapsed into, the primary comparison. A participant-level event indicator does not count repeated events in the same way as a rate outcome. A time interval addresses duration between changes rather than the occurrence rate itself. Therefore, apparent differences across these outcomes do not necessarily conflict; they may reflect distinct estimands and analysis methods.

The registry lists further secondary outcomes concerning the ratio of bolus to total insulin dose, interstitial glucose reduction following a non-meal-related correction bolus, and participants with severe hypoglycemic events. Numerical results for these outcomes are not reported in the registry record. Their absence from the posted results means no conclusion about their direction or magnitude can be drawn from this record.

Secondary analyses generally carry less weight than a designated primary analysis, especially when many outcomes are examined. In general, testing multiple outcomes increases the chance that some results will appear notable by chance unless the analysis plan addresses multiplicity. The registry does not report a multiplicity adjustment. The secondary findings should therefore be considered exploratory or supportive in interpretation, without treating an isolated result as definitive evidence about the broader treatment comparison.

Variation in the reported statistical methods also matters. The registry identifies an exact test, a rank-based test, and a mixed model for different secondary outcomes. Those methods target different data structures and summaries. The sponsor’s reported analyses and any recalculations should remain clearly distinguished, rather than being combined into one overall statistical claim.

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

• Percentage of Participants With at Least 1 Event of Infusion Set Failure
• Rate of Premature Infusion Set Changes
• Time Interval Until Infusion Set Change
• Ratio of Bolus/Total Insulin Dose
• Interstitial Glucose Reduction Rate From Hyperglycemia Following a Non-Meal-Related Correction Bolus Delivered Via the Pump
• Number of Participants With Severe Hypoglycemic Events

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison has two different statistical presentations, so it is important to distinguish them rather than treating them as duplicate reports of one estimate.

What does the rate ratio represent?

In general, a rate ratio compares the event rate in one treatment condition with the rate in a reference condition. A value below one indicates a lower estimated rate in the first condition; a value above one indicates a higher estimated rate. The recalculation uses the posted rates per 30 participant days and reports a rate ratio of 0.6 for LY900014 relative to insulin lispro. The calculation is unadjusted: it is not a reconstruction of a model that accounts for the trial’s crossover structure or any additional covariates.

The primary endpoint is a count of failures over exposure time. In general, count data can be analyzed with methods that account for the amount of time participants were observed. A Poisson approach is one such framework. Its assumptions can be important: in particular, if event counts vary more than the model expects, over-dispersion may make uncertainty estimates too narrow unless handled appropriately. The registry’s recalculation is marked as Poisson, but the registry does not report a dispersion estimate or enough detail to assess whether an alternative count model was considered.

Why is the sponsor’s analysis distinct?

The sponsor-reported primary analysis is a Wilcoxon signed-rank test, with the parameter described as median difference in final values. In general, the signed-rank test is a rank-based method for paired observations. That makes it a potentially relevant general type of method for paired or within-participant comparisons, but the registry record does not describe the exact paired values or how this test was applied to the stated event-rate endpoint. Its reported median difference and p-value are therefore best read as the sponsor’s stated analysis, not as a rate-ratio analysis.

A p-value is a measure of how compatible the data are with a specified null model under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. The recalculated p-value and the sponsor-reported p-value arise from different analysis presentations. The discrepancy means they should not be substituted for one another; the sponsor’s own analysis takes precedence.

What does the secondary analysis use?

The registry lists several distinct secondary outcome types. A participant-level percentage outcome records whether at least one qualifying event occurred, while an event rate retains information about repeated events and exposure time. A time interval outcome concerns the elapsed time until an infusion set change. These outcomes answer related but nonidentical questions, so their estimates and tests need not agree in direction or strength.

The sponsor-reported secondary methods include Prescott’s Exact test for the participant-level event outcome, Wilcoxon (Mann-Whitney) for the rate of premature infusion set changes, and mixed models analysis for time until infusion set change. In general, an exact test can be used for categorical outcomes when standard approximations may be unreliable; rank-based tests compare distributions without relying on a normal model; and mixed models can represent structured observations and account for specified sources of variation. These general descriptions do not establish the details of the actual models. The registry does not report the mixed model specification, its covariance structure, or the full analysis code or protocol.

The recalculated secondary comparisons are also unadjusted. For the continuous time-interval result, the recalculation uses the posted least-squares means and standard errors to estimate a mean difference. The registry’s own result instead reports a mixed-model least-squares mean difference and its confidence interval. Differences between the recalculation and sponsor analysis can reflect the use of summary-statistic approximations versus the sponsor’s model; the sponsor’s report is the primary record of that analysis.

What cannot be established from the record?

The registry record does not report the full statistical analysis plan, the original design assumptions, the treatment sequence details, or a description of any interim analysis. It also does not report whether all secondary analyses were prespecified or how missing observations were handled. As a result, the available results permit a careful description of the posted estimates and methods, but not a complete audit of the trial’s statistical conduct.

11. Confidence Intervals and Precision

The recalculated primary rate ratio is 0.6, with a 95% confidence interval from 0.437 to 0.824. In general, a confidence interval gives a range of estimates compatible with the data and the method used, under the interval’s assumptions. It conveys uncertainty in the estimated comparison; it is not a range containing a known proportion of individual outcomes, and it does not account for sources of uncertainty omitted by the analysis.

Here, the interval is attached to the unadjusted rate-ratio recalculation. It should not be mistaken for the confidence interval from the sponsor’s reported Wilcoxon analysis, which is given as 0.00 to 0.00 for the median difference in final values. These intervals concern different statistical summaries. The reported discrepancy makes it especially important to keep the estimand and method attached to each interval.

The sponsor-reported interval for the secondary time-interval analysis is from -5.3 to 1.7 hours around the least-squares mean difference of -1.8 hours. The recalculation for that outcome has a different interval, from -5.999 to 2.399 hours. The registry record does not report a sponsor confidence interval for every secondary comparison.

For the participant-level infusion set failure outcome, the recalculated risk difference interval extends from -0.110 to 0.066. In general, an interval spanning values on both sides of zero indicates that the data are compatible with effects in either direction under the calculation’s assumptions. It does not establish equivalence or prove that the treatments are identical.

Precision depends on the amount and structure of information, the outcome’s variability, and the analysis assumptions. The crossover design may create paired information, but the registry does not provide enough detail to evaluate how that structure contributes to the reported intervals. The recalculated intervals should therefore be interpreted as estimates from posted summaries, not as a substitute for fully documented sponsor analyses.

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 design justification. For these outcomes, the displayed planning values are participants per arm; they are not total event counts. The general assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculations consider an effect equal to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design that would have an 80% probability of detecting the specified effect if the planning assumptions and effect were correct. The 90% power column gives the corresponding illustration for a 90% probability. These are design-planning quantities, not descriptions of what the completed trial was certain to detect.

The rows considering 100%, 75%, and 50% of the observed effect show how the illustration changes when the target effect is smaller than the observed estimate. Smaller effects need more participants to detect under the same assumptions. The curve associated with these calculations should be read as a display of that planning relationship, not as evidence about the trial’s achieved power or a guarantee of future study performance.

These estimates use simplified assumptions, including equal allocation and a normal approximation. The crossover design and the endpoint’s event-rate structure may involve features that the illustration does not represent. The figures are useful for understanding how planning depends on the target effect and desired power, but they should not be read as observed power.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 18.2625; treatment rate λ₁ = 10.9575 events per patient-year; follow-up T = 0.11 years.
2. n = (1.96 + 0.842)² × (1/18.2625 + 1/10.9575) / (0.11 × [ln(0.600)]²) = 38.2, rounded up to 39 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
lambda0 <- 18.2625                      # control rate, events per patient-year
lambda1 <- 10.9575                      # treatment rate
tt      <- 0.114986584898429                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(3433677)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 39 (80% power), 52 (90% power)
 75% of observed effect: n per arm = 63 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 132 (80% power), 176 (90% power)
Simulated power, Poisson counts, n = 39 per arm: 0.819
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.645

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is a Wilcoxon signed-rank test of final values. It gives a median difference of 0.00, a 95% confidence interval from 0.00 to 0.00, and p = 0.375. The unadjusted recalculation instead compares posted event rates and gives a rate ratio of 0.6, with a 95% confidence interval from 0.437 to 0.824 and p = 0.002.

These results are not the same analysis expressed in different units. The recalculation is a simple comparison derived from the posted summary rates, whereas the registry’s reported result uses a rank-based test and describes a median difference in final values. The record does not explain the difference in endpoint representation or provide enough detail to reconcile the methods.

The discrepancy is flagged in the record. Accordingly, the sponsor’s own analysis takes precedence when describing the trial’s reported primary inference. The recalculation can still be useful as a transparent, unadjusted description of the posted rate summaries, but it must not be presented as if it supersedes the reported analysis. The registry does not report the full protocol or analysis plan that could clarify the intended estimand and the reason for the differing presentations.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, but does not report whether the testing plan adjusted for multiple comparisons. In general, when many outcomes are tested, the chance of obtaining at least one apparently unusual result can increase even if no corresponding underlying effect exists. Multiplicity procedures can control or otherwise address that issue, but the record does not describe such a procedure. Unadjusted secondary p-values should therefore be interpreted cautiously and not as if each were the only test conducted.

The full analysis plan is not reported in the registry record. The record does not specify which analyses were prespecified, whether any outcomes or methods changed, or whether an interim analysis was conducted. These details matter because prespecification and interim monitoring can affect how an analysis should be interpreted.

The primary analysis population is defined as all randomized participants who received at least one dose of study drug. The registry does not provide a full participant disposition or an explanation of how missing outcome data were handled. It does not report whether every randomized participant contributed observations to each analysis or how incomplete exposure periods were treated beyond the stated exposure calculation for the primary rate.

The crossover design makes treatment sequence and within-participant data structure relevant to the analysis. The registry identifies the study as crossover but does not report sequence allocation, period effects, or how these were incorporated into the sponsor’s primary analysis. It also does not report the original sample-size justification. These omissions limit assessment of how completely the posted analyses reflect the design and intended statistical questions.

These are reporting limitations, not proof that the trial did or did not use particular procedures. Where methods are not described, they are not reported in the registry record. The available record can support interpretation of the analyses it explicitly reports, but not assumptions about unreported safeguards or handling decisions.

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 (2.1%).

The serious adverse event counts are reported separately by treatment: 1 of 49 participants for LY900014 and 1 of 48 for insulin lispro. The registry reports 0 deaths in each treatment group. These are participant counts, not counts of all episodes or a measure of comparative risk adjusted for exposure. The record also identifies hypoglycaemia at 2.1% among the top serious adverse event terms, without specifying an arm-specific percentage in that listing.

The registry separately lists other, non-serious adverse event counts affecting 18 of 49 participants with LY900014 and 6 of 48 with insulin lispro. These counts should not be confused with serious adverse events. The record does not provide enough context to determine the nature, duration, or severity of every event, nor does it report a statistical comparison for these figures.

In general, adverse event counts describe what was recorded among participants in the study; they do not by themselves establish that a treatment caused an event. Differences in exposure, event definitions, and participant characteristics can matter. The figures should be read as descriptive registry results and not as a complete safety assessment or an individual treatment recommendation.

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

The statistics describe a randomized, double-blind crossover comparison of LY900014 and insulin lispro delivered by continuous subcutaneous insulin infusion in adults with type 1 diabetes. The primary endpoint focused on defined infusion set failures over a 6-week treatment period. The posted rate summaries and the sponsor’s reported statistical test do not produce the same inferential presentation, so the sponsor’s analysis takes precedence while the unadjusted rate-ratio recalculation remains separately identifiable.

The reported primary analysis does not establish that the treatments are equivalent. A nonsignificant p-value is not proof of no difference, and a confidence interval reaching or spanning a null value does not demonstrate that effects are identical. Conversely, a recalculated interval that lies on one side of the null does not resolve the discrepancy between the two analysis approaches. The estimand, method, and record-reported analysis must be considered together.

The findings are limited to the study conditions and outcomes described in the registry. They do not establish performance in other populations, devices, treatment durations, or settings. The registry record does not report the full protocol, detailed treatment sequence, complete analysis plan, or results for several secondary outcomes. Those gaps constrain broader interpretation.

The secondary outcomes cover distinct aspects of infusion set changes, insulin delivery, glucose response, and severe hypoglycemic events. Their results should not be merged into a single generalized claim about compatibility. The absence of numerical results for some listed outcomes means their implications cannot be assessed from this record.

Safety figures are descriptive and limited to the adverse event counts posted. They do not by themselves establish causality or encompass every possible safety consideration. Overall, the record is best read as a report of a specific trial and its stated analyses, with an important distinction between sponsor-reported inference and unadjusted recalculation. It does not support medical advice or a conclusion beyond the data and reporting limitations described.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definitions and analysis methods matter as much as a headline estimate. The primary outcome is an exposure-based event rate, while the sponsor-reported analysis is described as a Wilcoxon signed-rank test of final values with a median difference. A rate ratio and a median difference answer different statistical questions. Keeping the estimand attached to each result prevents a numerical comparison from being mistaken for a direct replication.

The crossover design is also relevant. In general, crossover studies can use within-participant comparisons to reduce the effect of stable differences between people, but the analysis needs to reflect the paired structure and any period or sequence features. The registry identifies the design but does not report enough detail to evaluate how those features were handled. That makes transparent reporting particularly important.

The primary endpoint’s exposure denominator provides a way to account for differences in time on treatment, while participant-level outcomes and time intervals offer complementary perspectives. Their coexistence shows that “infusion set performance” is not a single statistical quantity. Outcomes can be related clinically yet differ in definition, denominator, and method.

Finally, the discrepancy between recalculation and sponsor analysis demonstrates the value of comparing posted summary data with the trial’s reported inferential method without substituting one for the other. Confidence intervals and p-values are meaningful only in relation to the analysis that generated them. Clear documentation of populations, missing data, multiplicity, and model structure is essential for readers to assess precision and reproducibility.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record leaves important trial-specific details unreported. It identifies a crossover design but does not describe treatment sequence, period structure, washout arrangements, or handling of period effects. Those features can be relevant to interpreting a within-participant comparison, so their absence limits assessment of the design’s statistical implementation.

The primary outcome has a detailed event definition and exposure calculation, but the sponsor-reported test is described using median differences in final values. The record does not explain how that analysis corresponds to the stated event-rate endpoint. The recalculated rate ratio is unadjusted and cannot resolve that reporting gap. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence.

The original sample-size justification, full analysis plan, multiplicity approach, interim analysis details, and missing-data procedures are not reported in the registry record. Without these details, it is not possible to determine from the record whether the posted analyses follow all prespecified choices or how incomplete observations were addressed.

The trial enrolled 49 participants, with treatment-specific reported counts of 48 and 49 for the primary outcome. The registry does not explain the relationship between these counts and the crossover participant flow, nor does it provide complete outcome-specific disposition details. Small outcome counts can also make event-based estimates sensitive to a limited number of events; the record does not provide enough information to assess robustness under alternative models.

Several listed secondary outcomes have no numerical results reported in the registry record. The available results therefore offer an incomplete view of the broader set of outcomes named in the record. These limitations concern reporting and interpretation; they do not establish that unreported procedures or analyses were absent from the conduct of the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of LY900014 and Insulin Lispro With an External Continuous Subcutaneous Insulin Infusion System in Adult Participants With Type 1 Diabetes — NCT03433677.
• Registry record last updated 2019-10-08; status last verified 2019-10.
• Results first posted 2019-10-08.
• 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

NCT03433677 is a completed phase 3 randomized, double-blind crossover study of LY900014 and insulin lispro delivered by individualized continuous subcutaneous insulin infusion in adults with type 1 diabetes. The registry lists 49 participants enrolled and a 6-week treatment period for the primary outcome.

The primary endpoint was the rate of defined infusion set failures per 30 participant days. The sponsor-reported analysis and unadjusted rate-ratio recalculation differ in method and result; the sponsor’s analysis takes precedence. Secondary outcomes address other aspects of infusion set performance and treatment response, but numerical results for several are not reported in the registry record. Original design assumptions, multiplicity handling, and several analysis details are also not reported.