Effect of Insulin Degludec Versus Insulin Glargine on Glycemic Variability in Patients With Type 2 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Insulin Degludec Versus Insulin Glargine on Glycemic Variability in Patients With Type 2 Diabetes Mellitus (NCT02680457), a randomized phase 4 study. The primary outcome is Glycemic Variability: Mean Amplitude of Glucose Excursion (MAGE).

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, phase 4 crossover trial sponsored by the University of Guadalajara. The registry record lists enrollment of 12 and a completed status. The start is recorded as 2013-11, and primary completion as 2015-07.

In a crossover design, participants receive more than one intervention in a specified sequence, so each participant may contribute measurements under both interventions. The registry describes one sequence beginning with insulin degludec and another beginning with insulin glargine. Each insulin period lasted 6 days, with a 14-day washout between periods. The record does not report how participants were distributed between sequences or provide further details about the conduct of the washout.

The registry lists 12 participants for each primary outcome arm. Those arm figures should be read in the context of the crossover sequences, not as evidence that the study enrolled separate parallel groups. The registry record does not explain how the crossover structure was incorporated into the sponsor's statistical analysis.

The primary outcome was MAGE, measured during the last 48 hours of ambulatory continuous glucose monitoring over 3 days, starting on day 3 of administration. The registry also reports glucose area under the curve as a secondary outcome, with measurement every 5 minutes for 24 hours on day 5 post-dose. It notes that technical problems affected measurements and that baseline values for the primary measure were unavailable because of a design error. Further details about allocation procedures, masking procedures, participant flow, or the trial's original sample-size rationale 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.

Before assignment: Total number of patients: 12 in a crossover intervention. Interventions: 2. Washout period before the cross-over intervention. Protocol violations were detected at the end of the study in patients of both groups

Initial Intervention

Washout Period

Cross-over Intervention

Analysis population for the primary outcome, as defined in the registry: Comparison between both interventions. There are not baseline values of this measurements due to a design error. There were technical problems with the measurements.

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: Characteristics of the entire group

6. Primary Endpoint

The registry lists the primary outcome as Glycemic Variability: Mean Amplitude of Glucose Excursion (MAGE), measured over 2 days.

The primary endpoint was mean amplitude of glucose excursion (MAGE), expressed in mg/dl. It describes the mean size of interstitial glucose excursions during the specified monitoring period. Unlike a single glucose reading, a variability measure characterizes fluctuations across readings; in general, such a summary can capture the amplitude of changes over time rather than the level at one moment.

The registry defines the measurement window as the last 48 hours of ambulatory continuous glucose monitoring over 3 days, starting on day 3 of insulin administration. Continuous monitoring makes it possible to observe glucose values repeatedly across that window. MAGE was selected as the primary measure of glycemic variability, but the registry record does not report a justification for selecting it over other variability measures, a threshold for a clinically important difference, or a detailed calculation algorithm.

The record states that baseline values were unavailable because of a design error and that technical problems affected measurements. Consequently, the posted primary results are comparisons of the reported intervention-period values, not changes from a recorded baseline. The degree to which measurement problems affected the estimates is not reported in the registry record.

7. Results Posted in the Registry

• Insulin Glargine: mean 68.50 versus 75.20 on control; difference -6.70 (95% CI -41.39 to 27.99), standardized effect d = -0.15; z-test p = 0.705.

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.

Glycemic Variability: Area Under the Curve of Glucose

• 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 Glargine: mean 46,499 versus 46,776 on control; difference -277.00 (95% CI -14,546 to 13,992), standardized effect d = -0.02; z-test p = 0.970.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Insulin Glargine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome provides another summary of glycemic variability, using glucose area under the curve rather than MAGE. Across the posted secondary comparison, the two treatment summaries are close relative to their reported variability, and the sponsor's analysis does not indicate clear separation. The unadjusted recalculation likewise gives a result close to no mean difference, with uncertainty that is broad relative to the estimate.

This overall pattern is consistent with the primary endpoint in the limited sense that neither outcome shows a precise, clearly separated result in the posted data. The measures are not interchangeable, however: they summarize different aspects of glucose monitoring and use different measurement definitions. Agreement in their general pattern does not prove that the interventions have identical effects or that one measure validates the other.

The secondary outcome has fewer observations listed for degludec than for glargine. The registry does not explain why, whether missingness was related to participant characteristics or measurements, or how it was handled. That difference in available observations is relevant when interpreting the secondary comparison.

Secondary outcomes generally carry less evidential weight than a prespecified primary outcome, particularly when the record does not report a multiplicity strategy. In general, testing multiple outcomes without adjustment can increase the chance of chance findings. The registry does not state whether this outcome was confirmatory, how it was prioritized, or whether any multiplicity control was planned. It is therefore best viewed as supportive or exploratory context rather than independent confirmation of the primary finding.

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

• Glycemic Variability: Area Under the Curve of Glucose

9. Statistical Interpretation

10. Statistical Methods Explained

What does the sponsor-reported test compare?

The registry lists a Wilcoxon (Mann-Whitney) analysis for the primary comparison. In general, this is a rank-based method: it uses the ordering of observations rather than relying solely on means and standard deviations. It is commonly used to compare the distributions of two groups and can be less dependent on a normal-distribution assumption than a conventional mean comparison. A rank-based test does not automatically test a difference in means, and its interpretation depends on the shapes and distributions of the data.

The reported p-value is 0.630. In general, a p-value describes how unusual data at least as inconsistent with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, nor is it a measure of the probability that the result will replicate. A p-value that does not indicate clear evidence against the null does not demonstrate equivalence.

How does the recalculation differ?

The unadjusted recalculation uses the posted group summary statistics to describe a difference in means, along with its confidence interval and a corresponding p-value. It is a simple summary-based comparison, not a replacement for the sponsor's analysis. In general, a mean difference is sensitive to the magnitude of observations, while a rank-based method relies on their ordering. They can therefore give different numerical results without being contradictory.

The registry describes a crossover trial, but does not say whether the sponsor's analysis used paired participant-level measurements, adjusted for period or sequence, or otherwise accounted for repeated observations on the same participant. A conventional Wilcoxon-Mann-Whitney comparison is usually described for independent groups; in general, it does not by itself represent the pairing in a crossover study. The posted record does not include enough analytic detail to determine how the method was implemented or whether another model was used in addition.

Why does the crossover structure matter?

In a crossover study, measurements from the same participant can be correlated. General statistical methods for crossover data account for that dependence and may also consider treatment period and sequence. Treating related observations as independent can affect standard errors and inference. Conversely, an appropriate within-participant analysis can use the pairing to improve precision. Which approach is appropriate depends on the design, data, and prespecified analysis. The registry record does not report these details, so the summary results cannot resolve that methodological question.

The listed washout separates the treatment periods, but the record does not report evidence about whether carryover was assessed or how it was handled. In general, carryover means that an effect from an earlier treatment period may influence measurements in a later period. A washout is intended to allow prior treatment effects to dissipate, but its adequacy depends on the intervention and outcome; no conclusion about adequacy can be drawn from the registry information alone.

What does dispersion tell the reader?

The primary outcome is reported as a mean with standard deviation. In general, the mean describes the center of observed values, while the standard deviation describes how spread out individual values are around that mean. A standard deviation is not a confidence interval for the mean and does not show the full distribution of observations. With limited participant numbers, summary measures may not reveal skewness, outliers, or how many observations were unavailable.

The primary group standard deviations are 38.9 mg/dl and 47.4 mg/dl. These describe substantial variation among the observed values relative to the difference between the posted means. The registry does not provide participant-level data, a distribution plot, or further diagnostics that would show the shape of those observations.

How should secondary testing be read?

The secondary outcome is glucose area under the curve. Its sponsor-reported analysis is also listed as Wilcoxon (Mann-Whitney). In general, secondary outcomes can provide additional context, but testing several outcomes increases the chance that at least one result will appear notable by chance if no multiplicity strategy is used. The registry record does not report a multiplicity adjustment or an ordered testing plan. Secondary findings should therefore be viewed as exploratory unless stronger prespecification and multiplicity control are documented.

The registry does not report the original statistical analysis plan, the rationale for choosing the reported tests, adjustment variables, handling of missing values, or a detailed analysis population. Those omissions make it difficult to assess whether the posted analyses match the intended design and how robust the estimates are to alternative reasonable methods.

11. Confidence Intervals and Precision

The recalculated primary mean difference is -6.7 mg/dl for glargine relative to degludec, with a 95% confidence interval from -41.39 to 27.99 mg/dl. In general, a confidence interval gives a range of values reasonably compatible with the observed data under the calculation's assumptions. It is not a guarantee that the true value lies within the interval, and it does not assign a probability to each possible value after the data have been observed.

The interval spans zero and includes differences in either direction. Its breadth means the estimate is imprecise: the posted summary statistics do not pin down the size or direction of the mean difference closely. The central estimate alone should not be treated as definitive, especially when the interval also includes substantially different possible values. The registry record does not report a clinical importance threshold that would allow the interval to be judged against a defined meaningful effect.

The interval is an unadjusted recalculation from the posted summaries, not a confidence interval reported by the sponsor. It does not account for any participant-level pairing, sequence, or period terms unless those are implicit in the summary information; the registry does not report that such adjustments were made. General uncertainty from measurement problems and unavailable baseline values is also not captured by the interval itself.

The primary groups each have 12 observations listed, but the registry notes technical problems with measurements and does not give enough detail to establish how missing or unusable values were handled. The confidence interval should therefore be read as precision under the recalculation's assumptions, not as a complete account of all uncertainty in the trial.

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 assumptions. The registry record does not report the original sample-size justification. The posted planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

These figures are participants per arm, not total event counts. The columns for 80% and 90% power indicate the planned number of participants per arm for a hypothetical future study to have the corresponding chance of detecting the specified effect under the stated assumptions, if that effect and the other assumptions held. They are planning targets, not a guarantee that a study of that size will reach a particular result.

The rows that plan for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect illustrate how the assumed effect size changes the planning requirement. A smaller target effect is harder to distinguish from random variation, so it requires more participants under the same assumptions. The figures are derived from a very limited observed dataset, and the observed effect itself may be unstable; they should not be treated as a reliable forecast of a future study's needs.

This is not observed power. Observed power is not a useful substitute for interpreting the estimates and confidence intervals after a trial; these calculations instead show hypothetical planning requirements based on specified assumptions.

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 = -6.700; pooled standard deviation σ = 43.359.
2. n = 2 × (1.96 + 0.842)² × 43.359² / -6.700² = 657.4, rounded up to 658 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 <- -6.7                      # observed difference in means
sigma <- 43.3587938024111                     # 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(2680457)
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 = 658 (80% power), 881 (90% power)
 75% of observed effect: n per arm = 1,169 (80% power), 1,565 (90% power)
 50% of observed effect: n per arm = 2,630 (80% power), 3,521 (90% power)
power.t.test: 658.4 
Simulated power at n = 658 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor's primary analysis is reported as a Wilcoxon (Mann-Whitney) test with p = 0.630. The recalculation uses the posted means and standard deviations to estimate an unadjusted mean difference, its confidence interval, and a p-value. Because the methods and statistical quantities differ, their p-values need not match. The recalculation is not a correction to, or replacement for, the sponsor's own analysis.

The registry's discrepancy flag is false, so no conflict between the registry's reported analysis and the recalculated summary is identified by that check. The sponsor's reported test is the trial's own posted analysis. The recalculated mean comparison is best regarded as a separate descriptive lens, with assumptions that may not reflect the crossover pairing or other features of the sponsor's analysis.

The registry does not report enough detail to establish how the sponsor accounted for repeated measurements, treatment sequence, or period. It also does not provide a full analysis plan. Readers should therefore distinguish what is directly reported—the sponsor's rank-based p-value—from what the summary-statistic recalculation adds: an unadjusted estimate of a mean difference and its interval. Neither result establishes equivalence or clinical importance.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and a secondary glucose area-under-the-curve outcome, and it reports analyses for each. It does not report whether the analyses were prespecified in a statistical analysis plan, whether a hierarchy among outcomes was intended, or whether any adjustment for multiple testing was used. In general, when several hypotheses are tested, the chance of at least one apparently positive result can rise unless the testing strategy accounts for multiplicity. Without a reported plan, the strength of any secondary finding is harder to judge.

Missing-data handling is also not described in sufficient detail. The outcome record notes technical problems with measurements and absence of baseline values for MAGE because of a design error. The secondary outcome lists 11 observations for degludec and 12 for glargine, but the reason for the difference and the treatment of unavailable observations are not reported in the registry record. There is no description of imputation, exclusion rules, sensitivity analyses, or whether the available measurements represent all randomized participants.

The analysis population is not specified. The record does not state whether the reported results are based on all randomized participants, participants who completed both periods, or another defined group. It also does not detail participant withdrawals, adherence, protocol deviations, or exclusions. These omissions matter because excluding participants or measurements can affect comparability and precision, particularly in a crossover design where both treatment periods contribute information.

For crossover data, an analysis plan would ordinarily clarify how within-participant correlation, treatment period, sequence, and possible carryover are considered. The registry does not report those details. This does not establish that these issues were ignored; it means the record does not allow readers to verify how they were addressed. The uncertainty should temper conclusions based on the posted summary results.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event record lists no serious adverse events in either treatment group and no deaths. It lists other adverse events affecting 6 participants during the degludec group and 9 during the glargine group, with 12 at risk in each group as recorded. These are descriptive counts in a trial with limited enrollment, not precise estimates of comparative safety.

The registry does not provide serious adverse event terms because none are listed, and it does not give details about the nature, severity, timing, or relatedness of the other adverse events. It also does not report a statistical comparison of safety between treatments. The figures should therefore be read as the adverse-event counts posted in the record, not as evidence that either treatment is safer or that uncommon harms were ruled out.

In general, absence of a reported serious event in a small trial cannot establish that serious events cannot occur. The record's safety information is limited to the counts and categories described; further clinical interpretation is not supported by the registry data.

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

The registry records a randomized, double-masked crossover comparison of insulin degludec and insulin glargine in people described as drug-naïve with type 2 diabetes. The posted primary summaries and sponsor-reported test do not show a clear statistical separation in MAGE. The recalculated mean difference has a wide confidence interval that includes effects in both directions.

These results do not demonstrate that the treatments are equivalent. A finding that does not show clear evidence of a difference is not the same as evidence that the difference is negligible; an equivalence or non-inferiority conclusion would require an appropriate design, prespecified margins, and analysis, none of which are reported in the registry record. The record also does not give a threshold for a clinically important MAGE difference.

The data do not establish a treatment effect on clinical outcomes beyond the glucose variability measurements posted. The study record does not provide results for complications, longer-term glycemic control, quality of life, or other patient-important outcomes. The monitoring windows described are limited to short treatment periods.

Measurement problems, absent baseline values, incomplete information about missing observations, and unreported details of the crossover analysis further limit interpretation. The posted estimates should be read as uncertain summaries from this trial, not as a definitive ranking of the two insulins or as evidence that one should be selected over the other.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it uses a randomized crossover design to compare two interventions on a glucose-variability outcome. In general, crossover designs can make within-participant comparisons and may reduce the influence of differences between participants. That advantage depends on appropriate handling of repeated observations, period effects, sequence, and possible carryover; those analysis details are not reported in the registry record.

The record also illustrates the distinction between a test result and the precision of an estimated effect. The sponsor's rank-based test does not indicate clear separation, while the recalculated mean difference has a wide interval spanning both directions. Looking at the estimate and its uncertainty gives more context than treating a p-value alone as a verdict. Neither the p-value nor the interval establishes that the interventions are equivalent.

The sample-size planning illustrations make a further statistical point: planning around the observed effect can yield very different requirements depending on the effect size a future study aims to detect. Smaller effects require more participants under the stated assumptions. These are hypothetical planning calculations, not evidence about the power of this completed trial.

Finally, the registry notes technical measurement problems and missing baseline values, while leaving important analytic and missing-data details unreported. Such limitations are consequential in a small crossover dataset because both the quantity and structure of the available measurements affect precision. The record therefore offers a useful example of why design, analysis transparency, and uncertainty all matter when reading clinical trial results.

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.

Several limitations are specific to this record. The registry states that baseline MAGE values were unavailable because of a design error, so the posted primary comparison cannot be interpreted as a change from baseline. It also notes technical problems with measurements but does not describe their extent, timing, or effect on the analysis.

The study enrolled 12 participants, and the registry lists 12 observations in each primary treatment group. Such a limited dataset cannot estimate modest differences precisely, as reflected in the broad recalculated confidence interval. It also provides limited information about variability across a wider population. The number of observations alone does not resolve whether all randomized participants contributed usable measurements in both periods.

The crossover design makes details of analysis especially important. The record does not describe how the sponsor addressed within-participant pairing, treatment period, sequence, or carryover. It also does not report participant allocation across the two sequences, participant flow, adherence, or reasons for missing measurements. These gaps prevent a full assessment of how the design was reflected in the estimates.

The registry does not report the original sample-size rationale, detailed statistical analysis plan, analysis population, multiplicity strategy, or a clinically meaningful threshold for MAGE. The safety record gives counts but limited event detail. These limitations constrain conclusions about both efficacy measures and safety, and they make the posted results best viewed as preliminary descriptive evidence rather than a precise comparative estimate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Insulin Degludec Versus Insulin Glargine on Glycemic Variability in Patients With Type 2 Diabetes Mellitus — NCT02680457.
• Registry record last updated 2020-09-28; status last verified 2020-09.
• Results first posted 2020-09-28.
• 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, double-masked, phase 4 crossover trial sponsored by the University of Guadalajara. It lists enrollment of 12 and compares insulin degludec with insulin glargine, with 6-day treatment periods separated by a 14-day washout.

The primary endpoint was MAGE during the specified continuous-glucose-monitoring window. The sponsor reported a Wilcoxon (Mann-Whitney) comparison with p = 0.630. An unadjusted recalculation of the posted means estimates a difference of -6.7 mg/dl for glargine relative to degludec, with a 95% confidence interval from -41.39 to 27.99 mg/dl. The interval indicates substantial uncertainty.

The record also reports glucose area under the curve as a secondary outcome and adverse-event counts. It notes technical measurement problems and unavailable baseline MAGE values. Details on missing-data handling, the analysis population, the crossover analysis, and the original sample-size rationale are not reported in the registry record.