A Study of Nasal Glucagon (LY900018) in Japanese Participants With Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Nasal Glucagon (LY900018) in Japanese Participants With Diabetes Mellitus (NCT03421379), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Treatment Success During Controlled Insulin-Induced Hypoglycemia.

2. Clinical Question

3. Trial Design

The registry describes a completed Phase 3 randomized study of nasal glucagon compared with intramuscular glucagon in Japanese participants with diabetes mellitus. The study began on 2018-02-21, and primary completion was recorded on 2018-08-20. Enrollment was 75. These are distinct design and registry figures: enrollment is not the same as the primary analysis population, which required completion of both treatment visits and evaluable treatment-success data.

The design is identified as crossover and the masking as none. In a crossover study, a participant receives each treatment at different times, so the comparison can be made within participants as well as across treatment conditions. The registry record does not report the treatment sequence, any washout or interval between treatments, or details of how period effects were handled. It also does not report the randomization procedure beyond identifying allocation as randomized.

The two treatments were a single intranasal dose of 3 milligram (mg) glucagon nasal powder and a single intramuscular dose of 1 mg glucagon hydrochloride solution. The primary endpoint assessed treatment success from pre-dose up to 30 minutes after each administration. The analysis population is stated as all randomized participants who completed both visits and had evaluable treatment-success data. The registry reports 68 participants for each treatment in the primary results; it does not explain the difference between those analysis counts and the enrollment figure.

The primary objective was described as comparing efficacy and safety for insulin-induced hypoglycemia. Secondary outcomes covered pharmacodynamic and pharmacokinetic measures, including maximal blood glucose, time to maximal concentration, area under the concentration-versus-time curve, and maximal concentration. The registry record does not give further protocol detail for these assessments.

4. Participant Flow and Accounting

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

Before assignment: Participants were randomized to receive either nasal glucagon or intramuscular (IM) glucagon in the first period, followed by the alternate treatment in the second period.

Period 1

Reasons for not completing this period:

Washout Period (3 to 14 Days)

Period 2

Analysis population for the primary outcome, as defined in the registry: All randomized participant who completed both treatment visits and had evaluable treatment success data.

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 who received at least one dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Treatment Success During Controlled Insulin-Induced Hypoglycemia, measured over Pre-dose up to 30 minutes post each glucagon administration.

The primary endpoint is the percentage of participants achieving treatment success during controlled insulin-induced hypoglycemia. The registry defines success using either of two glucose criteria: plasma glucose reaching greater than or equal to 70 milligrams per deciliter (mg/dL), or an increase of at least 20 mg/dL from the plasma glucose nadir. In either case, the participant must not receive additional actions to increase plasma glucose concentration. Nadir is defined as the minimum plasma glucose concentration at the time of glucagon administration or within 10 minutes following administration.

The assessment period runs from pre-dose up to 30 minutes after each glucagon administration. A percentage endpoint gives a direct account of how many participants in the analysis population met the study's defined success criteria, rather than describing the size or timing of an individual glucose response. It is therefore a binary outcome at the participant level: each participant either meets the stated definition or does not.

Such a composite success definition can be useful for a treatment comparison because it incorporates a target glucose level and a specified increase from nadir, while also requiring that no additional glucose-raising action be used. The record does not report separate primary results for the two glucose criteria or for the two diabetes types. It reports the overall primary result for the described population. The endpoint by itself does not describe other aspects of glucose response, such as its full time course; those questions are addressed by secondary pharmacodynamic outcomes.

7. Results Posted in the Registry

• Glucagon Hydrochloride Solution: 100.0% (68/68) versus 100.0% (68/68) on control; risk difference 0.0 percentage points (95% CI 0.0 to 0.0), risk ratio 1.00 (1.00–1.00); unadjusted two-proportion z-test p = n/a.

8. Statistical Interpretation

9. Statistical Methods Explained

The statistical methods need to be read in the context of the endpoint and crossover design. The primary endpoint is binary: each participant either satisfied the treatment-success definition or did not. A percentage is the proportion of the analysed participants meeting that definition, expressed as a percentage. The registry reports 100.0% for each treatment, with 68 participants in each group. Because both reported percentages are at the ceiling of the scale, the observed difference in percentages is 0.0.

What does the unadjusted comparison represent?

The posted recalculation is an unadjusted comparison based on the reported binary summaries. It reports a risk difference of 0.0 and an interval from 0.0 to 0.0. A risk difference expresses the absolute difference between two event proportions. With identical observed proportions, the estimated difference is zero. This summary is straightforward to interpret, but it does not account for features of the crossover design unless those features are explicitly included in the calculation. The registry record does not state that the recalculation is a crossover-adjusted analysis.

At the boundary where all analysed participants have the event, standard uncertainty calculations based only on the observed event proportions can behave differently from methods designed for a crossover or non-inferiority analysis. In particular, the observed summaries contain no failures from which to estimate the usual within-group variation for this binary endpoint. A zero-width recalculated interval should therefore not be read as proof that the true difference is known without uncertainty. It reflects the simple recalculation's behavior with these posted summaries.

What does the sponsor analysis add?

The sponsor's analysis is labelled “Treatment Difference Wald's Method,” and is classified as non-inferiority. It reports an estimate of 0.00 and a 95% confidence interval from -1.47 to 1.47. A Wald confidence interval is generally formed by taking an estimate and extending in both directions according to its estimated standard error and a chosen confidence level. This general description does not establish the exact model used in this study. The registry record does not report a fuller statistical specification, the coding of treatment difference, or how the crossover structure was incorporated.

The sponsor's interval and the recalculated interval answer related but not identical statistical questions because they arise from different reported methods. The simple recalculation is based on the group-level binary summaries. The sponsor's analysis is the registry's stated non-inferiority analysis. Since the posted record does not indicate a discrepancy between the sponsor result and the posted data, the sponsor's reported result should be retained as the sponsor analysis rather than treated as an error. The interval should not be used to infer non-inferiority without the margin and decision rule.

Why does the crossover design matter?

In general, a crossover design can compare treatments within the same participant, potentially accounting for stable differences between participants. It also requires consideration of treatment period, sequence, and possible carryover effects. Whether those considerations are important, and how they were addressed, depends on the protocol and analysis. The registry record does not report sequence allocation details, a washout interval, or a model for period or carryover effects. It is therefore not possible to describe the sponsor's analysis as a particular paired or period-adjusted model based on the registry entry alone.

Randomization helps guard against systematic assignment differences, while the lack of masking means participants and study personnel were not masked according to the record. The record does not report whether endpoint assessment was masked or how the randomized sequence was generated. These are separate design details and should not be inferred from the general labels “randomized” and “none.”

How should planning illustrations be understood?

Sample-size planning is distinct from analysis of observed results. The planning assumptions describe a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation, with the effect to detect expressed as a fraction of the observed effect. The planning descriptions also distinguish participants per arm for ordinary outcomes from total events for time-to-event outcomes. These are planning illustrations based on an observed effect, not the trial's own design justification and not observed power. The registry record does not report the trial's sample-size justification, and no inference about the original design rationale can be made from a planning illustration.

In general, planning calculations depend on the chosen target effect, variability assumptions, error rate, and design. They do not show the probability that a completed trial has demonstrated a treatment effect. In this study, the observed primary percentages are identical, so any planning illustration based on the observed effect must be interpreted with particular care; the record does not provide the individual planning outputs or additional assumptions needed to explain them.

10. Confidence Intervals and Precision

The sponsor's reported treatment-difference estimate is 0.00, with a 95% confidence interval from -1.47 to 1.47. The interval describes a range of treatment-difference values compatible with the data and the sponsor's stated analysis method, under the assumptions of that method. A confidence interval is not a guarantee that the true effect lies in that range, nor does it assign a probability to individual values after the analysis. Its interpretation depends on the model and the design being appropriately represented.

The interval extends on both sides of zero. That is consistent with the estimated difference of 0.00 and indicates that the analysis does not locate the effect precisely at a nonzero value. Whether its limits are sufficiently narrow for a non-inferiority conclusion cannot be determined from the interval alone. The non-inferiority margin, the direction of the treatment difference, and a decision rule are not reported in the registry record. The interval therefore should not be translated into a yes-or-no non-inferiority conclusion.

The unadjusted recalculation gives an interval from 0.0 to 0.0 because both observed percentages are 100.0%. That degenerate interval is a consequence of the simple calculation applied to endpoint counts with no observed non-events. It is not evidence of perfect precision. The sponsor's interval reflects a different analysis and conveys uncertainty that the simple group-summary recalculation does not capture.

Precision is also limited by the information reported about the analysis population and design. The record identifies participants who completed both visits and had evaluable data, but does not explain exclusions from that population, report missing-data methods, or provide details of the crossover model. These omissions restrict independent assessment of how uncertainty was estimated. The posted results are most directly interpreted as a description of the analysed participants and the sponsor's stated interval, rather than as a complete account of all design and analysis assumptions.

11. Analyses Reported by the Sponsor

The registry reports the sponsor's analysis as a treatment-difference Wald method, classified as non-inferiority. Its estimate is 0.00, with a 95% confidence interval from -1.47 to 1.47. The record does not provide a p-value, the non-inferiority margin, or a complete model specification. Without the margin and decision rule, the reported interval cannot alone establish whether the study met its non-inferiority criterion.

The unadjusted recalculation from the posted binary summaries gives a risk difference of 0.0 and an interval from 0.0 to 0.0. This is a simple summary of identical observed percentages, not a replacement for the sponsor's stated analysis. The two intervals differ because the sponsor's analysis uses a method that is not reproduced by the group-level recalculation. The record does not provide enough detail to reconstruct that method or account for the difference fully.

The registry does not flag a discrepancy between the posted data and the sponsor analysis. The appropriate reading is therefore to report both results with their methods distinguished: the observed percentages and unadjusted recalculation describe the posted binary summaries, while the sponsor's interval is the reported non-inferiority analysis. No claim about the conclusion relative to a non-inferiority margin can be made from the registry record.

12. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and five posted secondary outcomes. The secondary outcomes concern pharmacodynamic and pharmacokinetic measures, including maximal blood glucose, time to maximal concentration, area under the concentration-versus-time curve, and maximal concentration. The record does not report a multiplicity adjustment, a testing hierarchy, or how the family of secondary analyses was handled. It is therefore not possible to determine from the registry entry whether or how the chance of false-positive findings across multiple outcomes was controlled.

The primary analysis population is described as randomized participants who completed both treatment visits and had evaluable treatment-success data. The record does not report the number excluded from this population, reasons for missing or unevaluable data, or an analysis of participants who did not complete both visits. It also does not report a missing-data imputation method or sensitivity analysis. The primary results should consequently be understood as applying to the stated evaluable population, not assumed to represent every enrolled participant.

The randomized crossover design also makes analysis-population definitions relevant. The registry does not report whether participants with only one evaluable treatment visit contributed to any analysis, how treatment periods were handled, or whether all randomized participants were analysed according to assigned sequence. These details are not reported in the registry record and should not be inferred from the population description.

The sponsor labels its primary comparison as non-inferiority, but the registry does not state the margin, the justification for that margin, or the precise decision rule. It also does not report interim analyses or the statistical plan in sufficient detail to establish whether such analyses occurred. The absence of those details in the registry record is not evidence that a procedure was or was not used; it means the procedure cannot be evaluated from this entry.

13. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: vertigo positional (1.4%).

The safety figures are reported for participants at risk in each treatment group. For nasal glucagon, the record lists 71 at risk for serious adverse events and 0 affected; for intramuscular glucagon, it lists 70 at risk and 1 affected. Deaths are listed as 0 in both groups. Other adverse events are listed for 15 of 71 at risk in the nasal group and 13 of 70 at risk in the intramuscular group.

The registry lists “Vertigo positional” at 1.4% among the top serious adverse-event terms. These figures should be read as registry safety counts, not as evidence that a treatment caused or prevented an event. The entry does not provide enough detail to determine timing, severity beyond the serious classification, relatedness assessment, or event-level overlap. The number at risk for safety reporting also differs from the primary analysis count, and the registry record does not explain that difference.

Safety summaries have a different purpose from the primary efficacy endpoint. The adverse-event counts describe reported events in the recorded safety populations; they do not establish comparative safety with precision, especially when the serious-event counts are sparse. The registry record does not report additional context such as exposure-adjusted rates or a detailed narrative of events.

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

The posted results show that treatment success, as defined in the registry, was recorded for 100.0% of participants in each treatment group in the primary analysis population. The unadjusted difference between those observed percentages is 0.0. The sponsor's analysis reports an estimate of 0.00 with a 95% confidence interval from -1.47 to 1.47. These are descriptive and inferential results from the study record, not a complete account of every possible treatment effect or outcome.

The identical percentages do not demonstrate that the treatments are interchangeable in all circumstances. A non-inferiority interpretation requires a prespecified margin and a rule for comparing the interval with that margin. Those details are not reported in the registry record. The sponsor's label of the analysis as non-inferiority should therefore be distinguished from a conclusion that can be independently verified using the registry entry.

The findings apply to the recorded primary analysis population: randomized participants who completed both treatment visits and had evaluable treatment-success data. They concern a controlled insulin-induced hypoglycemia setting and the assessment period from pre-dose up to 30 minutes after administration. The record does not establish how the results would apply to other populations, dosing circumstances, or settings.

Nor do the primary percentages describe every clinically relevant feature of glucose response. The registry lists secondary pharmacodynamic and pharmacokinetic outcomes, but their values are not included in the registry record of the primary result. The primary endpoint does not by itself characterize the speed or magnitude of response beyond its success definition, nor does it summarize all adverse events. Safety counts are reported separately and should be considered with their denominators and limited event detail.

In general, a completed randomized trial can inform a treatment comparison, but interpretation depends on the population analysed, the endpoint, the statistical method, and the precision of the estimate. Here, the record provides the primary percentages and a sponsor confidence interval, while leaving important details of the non-inferiority framework and missing-data handling unreported.

15. Why This Trial Matters Statistically

This trial illustrates how identical observed percentages can coexist with different statements about statistical uncertainty. Both treatment groups have a reported success percentage of 100.0%, giving an unadjusted risk difference of 0.0. A calculation based only on those group summaries produces an interval from 0.0 to 0.0. The sponsor's reported Wald interval, by contrast, extends from -1.47 to 1.47. Understanding what each result represents prevents the zero-width recalculation from being mistaken for certainty.

The crossover design is also statistically important. In general, crossover studies can use within-participant comparisons, but their analyses may need to account for treatment period and sequence. The registry identifies the design but does not report the detailed model or sequence information. That makes it especially important to distinguish the registry's sponsor analysis from a simple comparison of group-level percentages.

The non-inferiority label highlights another central principle: an estimate and confidence interval need a prespecified clinical or scientific margin to support a non-inferiority decision. The margin is not reported in the registry record, so the result cannot be independently classified against that criterion. Reporting the interval without inventing a threshold preserves the distinction between what is documented and what remains unknown.

Finally, the stated analysis population is narrower than the enrollment figure because it requires completion of both visits and evaluable endpoint data. The registry does not explain the difference. This is a reminder that endpoint percentages are meaningful only alongside a clear account of who contributed to the analysis and how missing data were handled. The record gives some, but not all, of that context.

16. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry entry leaves several trial-specific details unreported. Although the design is randomized and crossover, it does not describe the treatment sequence, interval between treatment visits, or handling of period and carryover effects. These details matter for understanding how a within-participant comparison was analysed. The entry also does not describe the randomization procedure beyond the allocation label or state whether endpoint assessment was masked.

The primary analysis population requires completion of both treatment visits and evaluable treatment-success data. The registry reports 68 participants for each treatment and an enrollment of 75, but does not explain the difference or give reasons for missing or unevaluable data. No missing-data method or sensitivity analysis is reported. As a result, the potential effect of excluding participants from the evaluable population cannot be assessed from this record.

The sponsor's analysis is identified as a Wald method and non-inferiority analysis, but the registry does not report its full model specification, the treatment-difference direction, the non-inferiority margin, or the decision rule. The sponsor's reported confidence interval therefore cannot be used to verify a non-inferiority conclusion from the registry information alone. The simple unadjusted recalculation is not a substitute for those missing details.

The record lists secondary pharmacodynamic and pharmacokinetic outcomes but does not provide their results in the registry record describing the primary outcome. It also does not report how multiplicity across outcomes was handled. Safety information includes event counts and a serious-event term, but lacks fuller event-level context. These limitations do not negate the posted primary observations; they define the scope of conclusions that can be drawn from the registry entry.

17. Related Tutorials

18. Related Statistical Calculators

19. Sources

• ClinicalTrials.gov: A Study of Nasal Glucagon (LY900018) in Japanese Participants With Diabetes Mellitus — NCT03421379.
• Registry record last updated 2019-10-08; status last verified 2019-09.
• 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.

20. Record Summary

This completed Phase 3 randomized, open-label crossover study compared a single intranasal dose of 3 milligram (mg) glucagon nasal powder with a single intramuscular dose of 1 mg glucagon hydrochloride solution in Japanese participants with diabetes mellitus. Enrollment was 75, and the primary analysis population required completion of both treatment visits and evaluable treatment-success data.

The primary endpoint was treatment success during controlled insulin-induced hypoglycemia, assessed from pre-dose up to 30 minutes after each administration. The registry reports 100.0% success for each treatment, with 68 participants per treatment. The sponsor's non-inferiority analysis reports an estimate of 0.00 and a 95% confidence interval from -1.47 to 1.47. The non-inferiority margin and several analysis details are not reported in the registry record.

Safety results list 0 serious adverse events in the nasal group and 1 in the intramuscular group, with 0 deaths in each. These counts and the primary endpoint describe the posted results; they do not resolve the unreported details of analysis, missing data, or the non-inferiority criterion.