Insulin Lispro 6 Days Versus Insulin Aspart 6 Days in Pump Use: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Insulin Lispro 6 Days Versus Insulin Aspart 6 Days in Pump Use (NCT01134107), a randomized phase 3 study. The primary outcome is Mean of Last Six 7-point Self Monitored Blood Glucose (SMBG) Taken on Day 6 for Insulin Lispro 6D and Insulin Aspart 6D Pump Reservoir In-use.

2. Clinical Question

3. Trial Design

This was a randomized, triple-masked, crossover trial listed as Phase 3. Participants continued to use their current insulin pump and received both insulin lispro 6D and insulin aspart 6D. Each treatment was used for 12 weeks, and chance determined the order. The registry record describes masking of the participant and study doctor; it does not further describe the roles included in the triple-masking designation.

The crossover structure means that each participant could contribute observations under both treatments, making within-participant comparison a central feature of the design. It can account for stable differences between people when treatment-period observations are analyzed appropriately. The registry record does not report the specific statistical model used for the primary analysis, including how it handled paired observations, treatment order, period effects, or any carryover effects. Those details are not reported in the registry record.

The trial enrolled 133 participants. The primary endpoint arm summaries each report 118 participants, while the primary analysis population definition also required completion of at least one post-randomization visit and at least one eligible Day 6 reservoir-cycle measurement. The reported primary outcome is an average over specified Day 6 readings in the final six weeks of each treatment period, rather than a single measurement or an average across the full treatment period.

The trial status is completed. The recorded start was 2010-11 and primary completion was 2011-12. The registry record lists four secondary outcome topics, including SMBG, daily insulin dose, HbA1c change, and the number meeting specified HbA1c thresholds. The original design assumptions, including any sample-size justification, are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Period 1-First Treatment Intervention

Reasons for not completing this period:

Period 2-Second Treatment Intervention

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who completed at least one post-randomization visit. Those included in the primary analysis had to have at least one reservoir in-use cycle with an SMBG measurement on Day 6 during the pre-specified collection period.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Mean of Last Six 7-point Self Monitored Blood Glucose (SMBG) Taken on Day 6 for Insulin Lispro 6D and Insulin Aspart 6D Pump Reservoir In-use, measured over Day 6 of each reservoir cycle for the last 6 weeks of each 12-week treatment period (Week 7 through Week 12).

The primary endpoint is the mean of the last six 7-point self-monitored blood glucose measurements taken on Day 6 of reservoir use. Measurements were collected during the final six weeks of each 12-week treatment period. The reported unit is millimoles per liter (mmol/L). The arm summaries give means of 8.83 for insulin lispro 6D and 8.43 for insulin aspart 6D, with standard deviations of 1.55 and 1.97, respectively.

A mean summarizes the central level of a continuous measure. In this setting, it provides a compact description of the recorded Day 6 SMBG values under each treatment. The standard deviation describes variation among the measurements included in each summary; it is not itself a measure of uncertainty in the difference between treatments.

Repeated glucose measurements can characterize a defined aspect of reservoir-period glucose readings. Restricting the endpoint to Day 6 and the last six weeks makes the estimand specific to that timing and collection window. It should not be treated as a summary of all glucose readings, all days of reservoir use, or all possible aspects of diabetes management. The registry record does not report further details about how multiple eligible cycles or missing Day 6 readings were handled beyond the stated inclusion requirement.

7. Results Posted in the Registry

• Insulin Aspart 6D: mean 8.43 versus 8.83 on control; difference -0.40 (95% CI -0.85 to 0.05), standardized effect d = -0.23; z-test p = 0.083.

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 to 12 Weeks for Each Treatment in Glycated Hemoglobin A1c (HbA1c) Values

• 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 deviations.
• Result:
  • Insulin Aspart 6D: mean -0.31 versus -0.16 on control; difference -0.15 (95% CI -0.28 to -0.02), standardized effect d = -0.29; z-test p = 0.022.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Insulin Aspart 6D than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover several aspects of treatment-period experience: SMBG, total, basal and bolus daily insulin dose, change in HbA1c, and whether participants achieve or maintain specified HbA1c thresholds. The registry record lists four secondary outcome topics and reports analyses across the outcomes. These endpoints broaden the description beyond the primary Day 6 SMBG summary, but they answer different questions and should not be treated as interchangeable measures of the same effect.

The reported HbA1c change summaries show mean changes from baseline of -0.16 for insulin lispro 6D and -0.31 for insulin aspart 6D. The unadjusted aspart-minus-lispro difference is -0.15, with a 95% confidence interval from -0.278 to -0.022 and an unadjusted p-value of 0.022. The sponsor analysis reports a least squares mean difference of 0.16 with a 95% confidence interval from 0.08 to 0.24. As with the primary endpoint, the registry record does not report enough detail about contrast direction and model specification to equate the sponsor estimate with the simple recalculation.

These HbA1c results concern a secondary outcome and do not replace the primary SMBG comparison. Nor do they independently settle the primary question: HbA1c and a specified Day 6 SMBG average measure different features and time frames. The registry record's multiple outcome measures and analyses raise the possibility of multiplicity, which can increase the chance of at least one apparently notable finding when many comparisons are examined. The record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting secondary outcomes. Consequently, unadjusted secondary p-values generally carry less confirmatory weight than a clearly prespecified primary analysis, and should be interpreted as supportive or exploratory evidence rather than as standalone proof.

The registry record does not provide secondary numerical results for every listed outcome in the registry record described for interpretation. Their inclusion in the outcome list should not be taken as evidence that a particular difference was observed. The overall pattern is therefore best described as a primary glucose comparison accompanied by additional, distinct outcomes, with inferential strength limited by the lack of reported multiplicity procedures and analysis details.

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

• Mean SMBG
• Mean Daily Insulin Dose (Total, Basal, and Bolus)
• Change From Baseline to 12 Weeks for Each Treatment in Glycated Hemoglobin A1c (HbA1c) Values
• Number of Participants Who Achieve or Maintain a Glycated Hemoglobin A1c (HbA1c) Less Than or Equal to 6.5% and Less Than 7%

9. Statistical Interpretation

10. Statistical Methods Explained

The statistical summaries distinguish the observed values in each treatment period from the estimated contrast between treatments. The reported arm means describe the average Day 6 SMBG for the participants included in each summary. Their standard deviations describe spread across observations. A standard deviation should not be read as a confidence interval: it captures variability in measurements, whereas a confidence interval expresses uncertainty about an estimated quantity.

What does the recalculated comparison represent?

The recalculated mean difference is an unadjusted contrast based on posted treatment summaries. It is reported as insulin aspart minus insulin lispro, with an estimate of -0.4 mmol/L. The accompanying 95% confidence interval is -0.852 to 0.052, and the unadjusted p-value is 0.083. This summary does not incorporate the within-participant pairing that is characteristic of a crossover trial. When observations from the same person are related, a paired analysis can use that relationship; treating arm summaries as if they were independent can fail to represent that design feature. The recalculation is useful as a transparent descriptive comparison, but the sponsor's analysis is the trial's reported inferential analysis.

A confidence interval gives a range of values compatible with the estimate under the statistical procedure and its assumptions. It reflects sampling uncertainty, not the range of individual participant measurements. Since the primary recalculated interval includes zero, it is compatible with no difference as well as with differences on either side of zero. The interval does not assign probabilities to individual values after the analysis, and it cannot establish that the treatments are identical.

How should the p-value be read?

The unadjusted p-value of 0.083 describes how unusual a result at least this extreme would be under a specified no-difference model and the assumptions used for the recalculation. It is not the probability that the no-difference model is true, nor is it a measure of the size or clinical importance of the difference. Because this is an unadjusted reanalysis of summary statistics, its p-value should not be substituted for a trial analysis that accounts for the crossover design.

The reported sponsor result is a least squares mean difference of 0.36 with a 95% confidence interval from 0.06 to 0.66. Least squares means are model-based estimates, and their contrasts can depend on the model and contrast direction. The registry record does not report the method, model specification, contrast direction, p-value, or non-inferiority margin. A reported interval that does not include zero may indicate a difference under the model and contrast used, but the stated non-inferiority or equivalence classification requires interpretation against a margin. Without the margin and analysis details, the record does not support a full reconstruction of that conclusion.

Why does crossover structure matter?

In a crossover study, participants receive both treatments in sequence. A suitable analysis can compare each participant's experience under the two treatments and account for features such as treatment period and sequence. The potential benefit is that each participant serves as their own comparison, which can reduce the influence of stable between-person differences. The tradeoff is that analysis must consider the design and assumptions about period effects and carryover. These features are not described in sufficient detail in the registry record to reproduce the primary model.

General statistical principle: if repeated measures within a participant are correlated, methods that account for that correlation generally estimate uncertainty differently from methods that assume independent observations. The simple arm-level recalculation omits that structure. Its confidence interval and p-value therefore answer a narrower, unadjusted question than a paired or model-based crossover analysis would.

What does non-inferiority require?

Non-inferiority asks whether an experimental treatment is not worse than a comparator by more than a prespecified clinically acceptable margin. Equivalence asks whether the difference lies within a prespecified range in both directions. These are not established merely by a non-significant test of difference. The margin, its justification, and the exact inferential procedure are essential to interpretation. The registry record labels the sponsor comparison as non-inferiority or equivalence but does not report the margin or method. No conclusion about the margin can be reconstructed from the listed confidence interval alone.

Finally, outcome interpretation should separate statistical evidence from clinical importance. The confidence interval addresses precision under a statistical model, while clinical importance depends on context and thresholds that are not reported for the primary SMBG endpoint. The trial record gives a focused set of glucose measurements and estimates; it does not establish implications beyond those measured outcomes.

11. Confidence Intervals and Precision

The recalculated primary contrast is -0.4 mmol/L, with a 95% confidence interval from -0.852 to 0.052. The interval spans zero, meaning the posted arm summaries are compatible with no difference under this unadjusted calculation. It also permits values favoring either treatment according to the aspart-minus-lispro direction of the contrast. The range is more informative than the point estimate alone because it communicates the uncertainty around that estimate.

Precision concerns the width of the interval, not whether an estimate crosses a significance threshold. A narrower interval would indicate less sampling uncertainty under the same model and assumptions; a wider interval leaves more possible values consistent with the data. Here, the interval does not isolate a single direction of difference. The fact that its upper limit is close to zero should not be converted into a claim of equivalence or no effect.

The arm-level recalculation does not preserve the crossover pairing, so its interval may not represent the precision of an analysis that uses within-participant observations. The registry's sponsor analysis reports a different quantity: a least squares mean difference of 0.36 with a 95% confidence interval from 0.06 to 0.66. The record does not report enough methodological detail to reconcile the estimates, including their contrast direction and model specification. Their intervals therefore need to be interpreted as results from separately defined analyses, not as competing measurements on an assuredly identical scale.

Confidence intervals quantify statistical uncertainty only within the analysis assumptions. They do not include every source of uncertainty, such as uncertainty about the appropriateness of the model, outcome selection, or missing-data handling. Those elements are not fully documented in the registry record. Precision should therefore be read alongside the design and reporting limitations, not as a complete statement of how firmly the result generalizes.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. They are illustrations calculated from the observed effect, rather than the trial's original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning row uses a specified fraction of the observed effect: 100%, 75%, or 50%.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the chosen effect under those assumptions, if that effect and model were correct. The 90% power column uses a higher target chance of detecting that same specified effect, and therefore gives larger planning counts. For the full observed effect, the figures are 309 participants per arm for 80% power and 413 per arm for 90% power. Planning for 75% of the observed effect gives 548 and 734 per arm, respectively. Planning for 50% gives 1,233 and 1,651 per arm.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the effect used for planning becomes smaller. These are planning illustrations, not observed power. They do not show the probability that this completed trial's result is correct, and they are not evidence that the original trial was designed around these assumptions. The original sample-size justification and design 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 = -0.400; pooled standard deviation σ = 1.772.
2. n = 2 × (1.96 + 0.842)² × 1.772² / -0.400² = 308.2, rounded up to 309 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 <- -0.4                      # observed difference in means
sigma <- 1.77248413251008                     # 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(1134107)
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 = 309 (80% power), 413 (90% power)
 75% of observed effect: n per arm = 548 (80% power), 734 (90% power)
 50% of observed effect: n per arm = 1,233 (80% power), 1,651 (90% power)
power.t.test: 309.2 
Simulated power at n = 309 per arm: 0.803 (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 registry record reports the sponsor's primary analysis as a least squares mean difference of 0.36, with a 95% confidence interval from 0.06 to 0.66. It classifies the analysis as non-inferiority or equivalence. The method, contrast direction, p-value, and non-inferiority or equivalence margin are not reported in the registry record.

The unadjusted recalculation from the posted arm summaries gives an aspart-minus-lispro difference of -0.4 mmol/L, with a 95% confidence interval from -0.852 to 0.052 and an unadjusted p-value of 0.083. This recalculation uses arm-level summary statistics and does not account for participant-level pairing or model adjustment. The sponsor's least squares mean contrast is a model-based result, so the two estimates should not be treated as interchangeable. In particular, their contrast orientation and estimands are not established as identical in the registry record.

The registry record does not flag a discrepancy between the recalculation and sponsor result. The sponsor analysis remains the trial's own reported analysis, while the recalculation is a separate, simple check based on posted summaries. The missing model details and margin limit independent assessment of the sponsor's non-inferiority or equivalence interpretation.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, treatment contrasts, or analyses. Even if each individual test uses a conventional significance threshold, conducting many tests increases the chance that at least one will appear statistically notable by chance. This is a general statistical concern, not evidence that any particular result in this trial is false.

The registry record lists the primary Day 6 SMBG measure and secondary outcome topics that include mean SMBG, daily insulin dose, HbA1c change, and HbA1c threshold attainment. It also records 14 outcome measures and 22 analyses. The record does not report whether the investigators adjusted for multiplicity, specified a testing hierarchy, or distinguished confirmatory from exploratory analyses. Those details are not reported in the registry record. The secondary unadjusted p-value should therefore be read cautiously and not as if it were the sole test in the study.

The primary analysis population is described as randomized participants who completed at least one post-randomization visit, with at least one qualifying Day 6 reservoir-cycle SMBG measurement required for inclusion in the primary analysis. The endpoint summaries report 118 participants for each treatment. The registry record does not explain in detail how missing readings, incomplete treatment periods, or multiple eligible reservoir cycles were handled, nor does it report sensitivity analyses addressing missing data.

In crossover studies, analysis populations and missingness can matter because participant-level comparisons rely on usable observations under both treatments or on a model that appropriately handles incomplete observations. The registry definition permits inclusion of participants with at least one post-randomization visit and at least one qualifying measurement, but it does not specify whether the primary model required complete paired outcome data or how it treated partial data. The exact primary model and its assumptions are not reported in the registry record.

These reporting gaps limit assessment of how robust the findings are to alternative missing-data assumptions and how the several analyses were interpreted together. They do not establish that the analysis was inappropriate; they mean the registry record does not contain enough detail to independently evaluate those decisions.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypoglycaemia (5.5%), diabetic ketoacidosis (0.8%).

The registry record lists serious adverse events for 127 participants at risk in each treatment group. It records serious adverse events affecting 3 participants during insulin lispro 6D and 7 during insulin aspart 6D. These are counts of affected participants as recorded, not a comparison adjusted for exposure time or crossover sequence. The record does not report deaths.

The listed serious adverse event terms include hypoglycaemia at 5.5% and diabetic ketoacidosis at 0.8%. The registry record does not specify an arm-specific breakdown for these terms in the registry record, so they should not be assigned to one treatment group. It also records other adverse events affecting 34 participants in the lispro group and 31 in the aspart group, with 127 at risk in each group.

These figures are descriptive safety summaries. They do not by themselves establish that one treatment caused more events, and raw counts do not account for timing, duration of exposure, repeated events, or individual differences. The record's safety summaries should be considered alongside the trial's size, crossover design, and the limits of the available reporting. They do not support broader safety conclusions beyond the events recorded.

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

The results describe a particular comparison in people with type 1 diabetes using their current insulin pump: a mean of specified Day 6 SMBG readings during the final six weeks of each 12-week treatment period. The arm summaries and unadjusted recalculation indicate a modestly lower recorded mean in the aspart period under the stated contrast direction, but the recalculated confidence interval includes zero. The registry's own model-based least squares mean result is reported separately and is classified as non-inferiority or equivalence.

These findings do not demonstrate that the two treatments are identical. A failure to establish a difference in an unadjusted comparison is not proof of no difference, while a non-inferiority or equivalence claim depends on a prespecified margin and an appropriate analysis. The margin and key model details are not reported in the registry record. The sponsor's reported result cannot therefore be fully evaluated from the available registry information alone.

The primary endpoint is not a comprehensive measure of glucose control or of every possible benefit and risk. It reflects a defined set of self-monitored glucose measurements at a specific point in reservoir use. Secondary HbA1c, insulin dose, and threshold outcomes address related but distinct questions. Multiple outcomes also require cautious interpretation when the multiplicity plan is not reported.

The study's crossover design can support within-person comparisons, but the simple recalculation does not retain that paired structure. The sponsor analysis is the trial's reported inferential analysis, although its method is not described in the registry record. The evidence should therefore be read as a set of reported summaries with limitations in precision and methodological detail, not as a definitive statement about all clinical outcomes or all circumstances of insulin pump use.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its crossover design makes the distinction between arm summaries and participant-level comparisons important. The same participants received both treatments, so the relationship between a participant's measurements across treatment periods can affect the estimated difference and its uncertainty. A simple recalculation from group means and standard deviations is transparent, but it cannot reproduce a paired or model-based analysis without participant-level information or further design details.

The primary result also illustrates why estimates, confidence intervals, and p-values should be read together. The recalculated point estimate alone gives a direction and scale, while its confidence interval shows uncertainty that includes zero. The p-value is not a probability that the treatments are equal, and a result that does not cross a conventional threshold cannot establish equivalence. Conversely, the registry's non-inferiority or equivalence label requires a margin and analysis details that are not reported.

Another important lesson is that outcomes are not interchangeable. A Day 6 SMBG average, HbA1c change, insulin dose, and threshold attainment address different aspects of the treatment periods. Their combined interpretation depends on prespecification and multiplicity handling, which the registry record does not describe. Statistical significance in a secondary analysis should not automatically outweigh an uncertain primary comparison.

Finally, the planning illustrations are not retrospective evidence of trial power. They show how hypothetical sample-size requirements change under stated assumptions and effect fractions. The original design rationale is not reported, so those illustrations cannot be used to judge whether the trial was adequately planned. Together, these features make the record a useful example of how study design, estimand, uncertainty, and reporting completeness shape interpretation.

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 primary summaries and recalculation are based on arm-level statistics, not participant-level crossover data. The recalculated comparison therefore does not preserve within-person pairing, and it may not match the trial's model-based estimand or uncertainty. The registry record identifies a sponsor least squares mean contrast but does not report the model, contrast direction, covariance handling, or other details needed to reproduce it.

The sponsor result is labeled as non-inferiority or equivalence, but the margin and its rationale are not reported in the registry record. Without that information, the statistical basis for that classification cannot be fully assessed. The reported confidence interval alone is not enough to establish the intended non-inferiority or equivalence criterion.

The primary endpoint is limited to Day 6 measurements in the last six weeks of each treatment period. It does not summarize every measurement during reservoir use or the entire treatment period. The registry record does not describe the number of eligible cycles per participant, the detailed handling of multiple readings, or missing outcome data. Nor does it report sensitivity analyses for missingness or a complete account of the analysis population used in the sponsor's model.

Multiplicity is another limitation: several outcomes and analyses are recorded, but the adjustment strategy or testing hierarchy is not reported. Secondary findings should consequently be interpreted with caution. The trial enrollment was 133, while the endpoint summaries and safety summaries use different recorded group counts; the registry record does not fully explain all transitions between these populations. Finally, the trial evaluates specified glucose and safety summaries over treatment periods. The registry data described do not support conclusions about unreported outcomes or broader contexts beyond the studied measures and participants.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Insulin Lispro 6 Days Versus Insulin Aspart 6 Days in Pump Use — NCT01134107.
• Registry record last updated 2013-04-11; status last verified 2013-04.
• Results first posted 2012-10-26.
• 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 record describes a completed, randomized, triple-masked, crossover Phase 3 trial of insulin lispro 6D versus insulin aspart 6D in people with type 1 diabetes using insulin pumps. Participants received each treatment for 12 weeks in an order assigned by chance. The primary endpoint was the mean of the last six 7-point SMBG measurements taken on Day 6 during the final six weeks of each treatment period.

The arm summaries report means of 8.83 mmol/L for lispro and 8.43 mmol/L for aspart. The unadjusted recalculated contrast is -0.4 mmol/L, with a 95% confidence interval from -0.852 to 0.052 and p = 0.083. The sponsor analysis reports a least squares mean difference of 0.36, with a 95% confidence interval from 0.06 to 0.66, and is classified as non-inferiority or equivalence. The model details and margin are not reported in the registry record.

Secondary outcomes include glucose, insulin dose, and HbA1c measures. Interpretation is constrained by missing analysis details, unreported multiplicity and missing-data procedures, and the unadjusted recalculation's failure to retain crossover pairing.