A Trial Comparing the Safety and Efficacy of Insulin Degludec and Insulin Glargine, With or Without OADs in Subjects With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial Comparing the Safety and Efficacy of Insulin Degludec and Insulin Glargine, With or Without OADs in Subjects With Type 2 Diabetes (NCT02030600), a randomized phase 3 study. The primary outcome is Number of Treatment Emergent Severe or BG Confirmed Symptomatic Hypoglycaemic Episodes During the Maintenance Period.

2. Clinical Question

The trial’s title and summary frame the comparison around safety and efficacy, while its primary endpoint is specifically a count of hypoglycaemic episodes during designated maintenance periods. The result therefore addresses that endpoint and timeframe, rather than every aspect of safety, glucose control, or treatment experience. The registry record also lists other outcomes, including severe hypoglycaemia, adverse events, HbA1c, and fasting plasma glucose. Those outcomes provide additional perspectives, but they are distinct from the primary count outcome and should not be treated as interchangeable measures.

3. Trial Design

This was a phase 3, randomized, double-blind, crossover trial comparing insulin degludec with insulin glargine in people with type 2 diabetes. Participants were assigned to one of two treatment sequences: IDeg followed by IGlar, or IGlar followed by IDeg. Both treatments were once daily and could be used with oral anti-diabetic drugs. The registry summary excludes sulfonylureas and glinides from the oral-drug context.

Each treatment period lasted 32 weeks. The total trial duration for an individual participant could be up to 67 weeks. The primary endpoint was evaluated after 16 weeks of treatment in each period, during Week 16–32 and Week 48–64. The record reports enrollment of 721 participants and describes the trial as completed. Its recorded start date is 2014-01-06, and its primary completion date is 2015-12-04.

A crossover design differs from a parallel-group design because participants receive both treatments in sequence. The comparison can therefore draw on information from treatment periods within the same participant, although the precise model and handling of within-participant dependence matter for interpretation. The registry reports a Poisson method for the primary comparison, but the detailed model specification, including how the crossover structure was handled, is not reported in the registry record.

The record identifies randomization and double masking, but does not describe the randomization procedure, the success of masking, a washout period, or how period and sequence effects were assessed. It also does not report a sample-size justification or the protocol’s full statistical analysis plan. Those details should not be inferred from the design label or from the posted results.

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.

Treatment Period 1

Reasons for not completing this period:

Treatment Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The trial followed a cross over design. Descriptive analysis was based on the safety analysis set (subjects receiving at least one dose of the investigational product or its comparator). Number of subjects analysed=subjects with available data for the endpoint as per individual trial products. Statistical analysis was performed on full analysis set

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: Full analysis set included all randomised subjects. One subject was excluded from the analysis due to unsigned casebook.

6. Primary Endpoint

The registry lists the primary outcome as Number of Treatment Emergent Severe or BG Confirmed Symptomatic Hypoglycaemic Episodes During the Maintenance Period, measured over After 16 weeks of treatment, in each treatment period (Week 16-32 and Week 48-64).

The primary endpoint counts treatment-emergent severe or blood-glucose-confirmed symptomatic hypoglycaemic episodes during the maintenance period. The registry defines an eligible episode as severe and/or confirmed by a plasma glucose value of <56 mg/dL (3.1 mmol/L), with symptoms consistent with hypoglycaemia. An event was considered treatment-emergent when its onset was on or after the first day of exposure to randomized treatment and no later than the last day of randomized treatment.

The endpoint is a count, not simply the proportion of participants who experienced any episode. A participant may contribute more than one event, so the count can reflect both how many participants have episodes and whether some participants experience repeated events. The maintenance-period window focuses the assessment on the later part of each treatment period, after 16 weeks of treatment, rather than counting events across the entire trial.

Counting recurrent events is useful when the frequency of episodes is clinically and statistically relevant. It preserves information that would be lost by reducing the outcome to yes or no for each participant. At the same time, counts can be influenced by differences in participants’ observation time and by repeated events within individuals. The posted description does not provide the full model specification or an event-rate denominator, so those aspects cannot be assessed from the registry record alone.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

What does a treatment ratio express?

A treatment ratio compares the modeled event count or rate under one treatment with that under another. A value of 1 represents no relative difference on the ratio scale; a value below 1 represents a lower estimated count or rate for the treatment in the numerator, given the model’s definitions. The sponsor reports a ratio of 0.70, with IDeg and IGlar as the two treatments in the comparison. This is a relative measure. It does not directly state the number of episodes avoided for an individual participant, and it does not indicate how events were distributed among participants.

The ratio comes from a Poisson analysis. Poisson models are commonly used for count outcomes, where observations can take non-negative integer values and event frequency is of interest. A count model can make use of the number of events rather than reducing each participant’s outcome to whether any event occurred. However, a Poisson model relies on assumptions about the relationship between the expected count and its variability. The record identifies the method but does not report enough model detail to evaluate its specification or assumptions.

Why can over-dispersion matter?

In a basic Poisson model, the variance is linked to the mean. Clinical event counts may vary more than that assumption allows, for example when some participants have many events and others have few or none. This is called over-dispersion. If a model does not account for over-dispersion when it is present, uncertainty estimates can be too narrow. Alternative variance approaches or count models can address some forms of extra variability. Whether the sponsor assessed or adjusted for over-dispersion is not reported in the registry record, so no conclusion about that issue can be drawn from the method label alone.

What does the confidence interval add?

The 95% confidence interval for the treatment ratio is 0.61 to 0.80. A confidence interval describes uncertainty in the estimated comparison under the analysis method and its assumptions. It is not a range that guarantees the true value lies inside it, nor is it a prediction interval for an individual participant’s outcome. The interval’s location relative to 1 helps interpret the ratio-scale comparison. The p-value, reported as < 0.001, provides a related test against a ratio of 1 under the sponsor’s analysis. Neither statistic measures clinical importance by itself.

How does the crossover design affect analysis?

Because participants received both treatments in sequence, outcomes may be correlated within a participant. A suitable analysis may need to account for that dependence, as well as treatment period and sequence. The registry reports a Poisson method for the primary endpoint, but does not specify whether or how these crossover features were included. It also does not report the assessment of carryover effects or the details of the model’s covariance structure. Those missing details prevent a full independent reconstruction of the sponsor’s analysis.

The endpoint description identifies a safety analysis set made up of participants who received at least one dose of an investigational product or comparator, with available data for the endpoint. The stated analysis-set counts are 632 for IDeg and 618 for IGlar. The registry does not give a complete accounting of endpoint missingness or explain how unavailable observations were handled. In a crossover trial, availability may differ across treatment periods, but the reasons for any missing data are not reported.

What can recalculation add?

A recalculation from posted summary statistics can provide a transparent, unadjusted comparison for outcomes where the summaries allow it. It is not necessarily equivalent to the sponsor’s model, particularly when the analysis uses the crossover structure or adjusts for other factors. For the primary count outcome, the registry’s skip note indicates that values were missing or not estimable for a two-arm comparison from the posted summary statistics. Therefore, no independent simple recalculation is available for that primary endpoint, and the sponsor’s reported Poisson analysis is the relevant posted comparison.

The registry also includes planning illustrations for the binary secondary outcome. Those illustrations use a two-sided significance level of 0.05, equal allocation, a normal approximation, and effects set to specified fractions of the observed effect. They are planning examples based on an observed contrast, not the trial’s own design justification and not observed power. The sample sizes in such illustrations describe hypothetical future planning under those assumptions; they do not alter the evidence from the completed trial.

10. Analyses Reported by the Sponsor

For the primary count endpoint, the sponsor reports a Poisson-model treatment ratio of 0.70, a 95% confidence interval from 0.61 to 0.80, and p < 0.001. The registry also posts descriptive event counts and participant counts by treatment. However, it indicates that values were missing or not estimable for a two-arm recalculation of this count outcome from summary statistics. Consequently, there is no independent unadjusted recalculation to set beside the sponsor’s primary estimate.

The sponsor’s modeled result is therefore the principal posted comparison for the primary endpoint. It should be interpreted according to the model and population described in the record, while recognizing that the full statistical specification is not reported. A model-based treatment ratio and a raw count comparison are not interchangeable: they may use different information and address the data differently, especially in a crossover trial with recurrent events.

For the secondary binary outcome concerning one or more severe episodes, the registry reports a McNemar analysis and a p-value of 0.346. The unadjusted recalculation based on posted summaries is a separate analysis. The record does not identify a discrepancy flag for the analyses. Even so, the sponsor’s own analysis should be interpreted in the context of its paired crossover design, whereas a simple recalculation from group summaries does not necessarily reproduce the sponsor’s analysis structure. These results should not be merged into a single estimate or treated as if they arose from identical methods.

11. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcomes, but does not report a multiplicity-control strategy for the primary and secondary analyses. When researchers examine several outcomes or make several statistical comparisons, the probability of at least one result appearing statistically notable can increase. A prespecified testing hierarchy or an adjustment method can address that issue, but the appropriate approach depends on the trial’s intended claims. Without the protocol or analysis plan, it is not possible to determine which secondary tests were confirmatory, whether a hierarchy was used, or whether any adjustment was applied.

Missing-data handling is also not described in enough detail for assessment. The primary analysis description refers to a safety analysis set and participants with available endpoint data. It does not report the reasons observations were unavailable, the number missing by treatment period, or the method used to address missing outcome data. The endpoint counts differ by treatment, but the record does not explain the difference. It would be inappropriate to assume that missingness was random or that a particular imputation approach was used.

The record identifies a crossover design and reports a Poisson method for the primary count outcome. It does not report whether the model included period, sequence, participant-level effects, or a treatment-by-period term. It also does not describe any assessment of carryover or washout. These are relevant features because treatment periods within a participant are not generally independent observations.

The available population description for the primary analysis is the safety analysis set: participants receiving at least one dose and with endpoint data available. A full description of other analysis populations, including any protocol-adherent or intention-to-treat definitions, is not reported in the registry record. The sample-size justification and interim-analysis plan are also not reported. Those gaps constrain evaluation of the analysis choices, but do not invalidate the posted estimates; they define what can and cannot be assessed from the registry information.

12. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypoglycaemia (1.4%), angina pectoris (0.6%), sepsis (0.6%), coronary artery disease (0.5%), non-cardiac chest pain (0.5%).

The adverse-event summary reports serious events for 64 of 671 participants at risk in the IDeg group and 65 of 665 at risk in the IGlar group. For other adverse events, it reports 93 of 671 and 77 of 665, respectively. These are descriptive counts within the registry’s adverse-event summary. They are not adjusted comparisons, and the record does not provide a statistical comparison for these figures. They should not be read as proof of equivalence or as a complete accounting of relative safety.

The registry lists hypoglycaemia, angina pectoris, sepsis, coronary artery disease, non-cardiac chest pain, and unstable angina among the most frequent serious-event terms, with percentages as posted. The record does not provide enough detail in this summary to interpret those terms as treatment-caused events or to compare their risk formally. A term’s appearance in a serious-event list does not establish causation.

Deaths are not reported in the registry record. The adverse-event counts also use a different set of at-risk denominators from the primary endpoint analysis population. They should not be substituted for the primary hypoglycaemia analysis or interpreted as the same outcome.

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

The primary result describes a modeled comparison of treatment-emergent severe or blood-glucose-confirmed symptomatic hypoglycaemic episode counts during the maintenance portions of the treatment periods. The sponsor’s estimated treatment ratio is below 1, with a confidence interval that also lies below 1. This supports a difference in the modeled count comparison under the sponsor’s analysis, for the population and periods described in the registry.

It does not mean that every participant had fewer episodes, that the same relative difference applies to each person, or that every kind of hypoglycaemia was measured. It does not describe the full course of treatment outside the maintenance windows. The endpoint counts events, and recurrent episodes may contribute more than once to the total. The posted summary does not show how events were distributed among participants.

The result also does not establish a broad conclusion about every safety outcome or glucose-control measure. The registry lists secondary endpoints and adverse-event information, but those measures have different definitions and analyses. Their interpretation depends on the outcome, uncertainty, and the unreported multiplicity plan. The record does not report the full statistical analysis plan, missing-data procedures, or detailed handling of crossover effects, so the robustness of the primary estimate to alternative analytical choices cannot be evaluated from the registry alone.

Finally, a statistically notable result is not by itself a measure of clinical importance. The treatment ratio is a relative model estimate, and the record does not provide a single absolute event-rate contrast adjusted for the analysis structure. The posted data support interpretation of the specific primary comparison, not claims beyond its endpoint, time window, and analysis context.

14. Why This Trial Matters Statistically

This trial illustrates why the statistical form of an endpoint matters. The primary outcome is a recurrent-event count, while a related secondary outcome asks whether a participant experienced at least one severe episode. The count retains information about repeated episodes; the binary measure does not. Each can be useful, but each summarizes a different feature of the experience and may lead to different estimates and precision.

The crossover structure also makes the analysis more than a comparison of two independent groups. Participants received both treatments in different sequences, so a careful analysis may need to reflect dependence within participants and potential period effects. The sponsor’s primary analysis uses a Poisson method, but the registry does not provide the detail needed to see precisely how the design was represented in the model. This is an important distinction between knowing the named statistical method and knowing its complete implementation.

The record additionally shows the limits of independent recalculation from summary data. Descriptive counts alone do not reproduce a crossover count model, and the registry notes that a two-arm recalculation was not available for the primary outcome. That underscores why model-based results should be interpreted with their analysis population, model assumptions, and uncertainty—not reduced to a comparison of raw totals.

Finally, the trial demonstrates the importance of complete reporting. Multiplicity, missing-data methods, sample-size justification, and crossover-model details affect how readers assess the strength and scope of findings. When those details are not reported in the registry record, a precise reading separates what the posted analysis estimates from what cannot be independently assessed.

15. 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.

Several limitations are specific to the information reported for this trial. The primary endpoint is evaluated in maintenance windows within two treatment periods, so it does not summarize the entire treatment experience. The registry defines treatment-emergent events by their onset relative to exposure, but does not provide participant-level event distributions or explain whether exposure time was incorporated as an offset in the count model.

The crossover design may require explicit handling of within-participant correlation, period, sequence, and possible carryover. The registry gives the design and names a Poisson analysis, but does not report the model specification or diagnostic checks. A washout period and any carryover assessment are not reported in the registry record. This limits independent evaluation of whether the posted model fully reflects the design.

The primary analysis description is truncated after its reference to the safety analysis set and endpoint availability. It does not provide a complete account of the analysis population or missing observations. The reason the endpoint analysis counts differ by treatment, and the treatment of unavailable data, are not reported. These omissions leave uncertainty about the contribution of incomplete follow-up or differing data availability.

The record does not report the sample-size justification, interim analyses, or full statistical analysis plan. It also does not report a multiplicity strategy for the several outcomes. Without these details, readers cannot establish which analyses were planned as confirmatory, whether secondary testing was adjusted, or how the primary analysis choices were settled in advance. The registry’s posted estimates remain interpretable as reported, but their broader inferential context is incomplete.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: A Trial Comparing the Safety and Efficacy of Insulin Degludec and Insulin Glargine, With or Without OADs in Subjects With Type 2 Diabetes — NCT02030600.
• Registry record last updated 2019-05-10; status last verified 2019-04.
• Results first posted 2017-01-30.
• 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.

19. Record Summary

This completed phase 3 trial randomized 721 participants in a double-blind crossover comparison of once-daily insulin degludec and insulin glargine, with or without oral anti-diabetic drugs. Each treatment period lasted 32 weeks, and the total duration for an individual participant could be up to 67 weeks.

The primary endpoint counted treatment-emergent severe or blood-glucose-confirmed symptomatic hypoglycaemic episodes during the maintenance periods. The sponsor reported a Poisson-model treatment ratio of 0.70, with a 95% confidence interval from 0.61 to 0.80 and p < 0.001. The registry does not permit a simple two-arm recalculation of that count result from the posted summary statistics.

Other posted information covers severe hypoglycaemia, adverse events, HbA1c, and fasting plasma glucose. Important details about multiplicity, missing-data handling, sample-size justification, and the complete crossover model are not reported in the registry record. The primary estimate should therefore be understood as the sponsor’s modeled result for the stated endpoint and analysis context.