Comparing Efficacy and Safety of Insulin Degludec/Insulin Aspart Twice Daily and Biphasic Insulin Aspart Twice Daily in Subjects With Type 2 Diabetes Mellitus Before, During and After Ramadan: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing Efficacy and Safety of Insulin Degludec/Insulin Aspart Twice Daily and Biphasic Insulin Aspart Twice Daily in Subjects With Type 2 Diabetes Mellitus Before, During and After Ramadan (NCT02648217), a randomized phase 3 study. The primary outcome is Change in HbA1c (%) (Glycosylated Haemoglobin).

2. Clinical Question

The comparison concerns a specific time window around Ramadan, rather than a general comparison across all circumstances or a long-term outcome. The registry also lists fasting plasma glucose, fructosamine, target attainment and hypoglycaemia outcomes as secondary measures. Those outcomes provide other ways to describe glycaemic measures and treatment-emergent events, but they do not replace the stated primary question. The record describes the trial as completed, randomized, open-label and parallel-group. It does not report the specific eligibility criteria or the clinical rationale for choosing the treatment regimens beyond the stated aim of comparing their efficacy and safety before, during and after Ramadan.

3. Trial Design

The registry describes a completed, randomized, open-label, parallel-group phase 3 trial. It lists an enrollment of 263 participants and identifies the setting as Africa and Asia. Participants were assigned to insulin degludec/insulin aspart or biphasic insulin aspart; both are described in the trial aim as twice-daily regimens. The registry does not report the allocation ratio or the method used to generate or conceal the random assignment.

The primary outcome was change in HbA1c from week 0 to the end of Ramadan, identified as day 29 of Ramadan. For the primary result, the record reports 121.0 participants analyzed in the insulin degludec/insulin aspart group and 124.0 in the biphasic insulin aspart group. The primary outcome description clarifies that the analyzed number counts participants who contributed to that analysis. The registry does not describe why the analyzed numbers differ from the enrollment total, or give a fuller account of withdrawals, missing observations or analysis populations.

The sponsor-reported analysis used a mixed model for repeated measurements and is presented as a treatment contrast. The registry does not report the model specification, its covariance structure, included covariates or handling of missing data. The primary outcome is reported as a least-squares mean with standard error, while the secondary continuous outcomes are reported as means with standard deviations. These are different summaries and should not be treated as interchangeable.

The record gives a start date of 2016-01-04 and a primary completion date of 2016-09-04. It does not report the trial's original sample-size assumptions, a detailed analysis plan, interim analyses or a multiplicity strategy. Those design details therefore cannot be inferred from the outcome estimates.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Here, 'number of subjects analysed' specifies the number of subjects, who contributed to the analysis.

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: Baseline results are based on the full analysis set (FAS), which included all randomised subjects.

6. Primary Endpoint

The registry lists the primary outcome as Change in HbA1c (%) (Glycosylated Haemoglobin), measured over From week 0 to end of Ramadan (day 29 of Ramadan).

The primary endpoint is change in HbA1c, expressed as a percentage of HbA1c, from week 0 to the end of Ramadan on day 29 of Ramadan. HbA1c is a measure of glycaemia over time, so a change from baseline describes how the group average differed at the specified endpoint compared with the start of follow-up. The registry defines the outcome as mean change and reports least-squares means for the treatment groups.

Using a change measure focuses the comparison on movement over the defined study period, rather than only comparing endpoint values. The treatment contrast then summarizes the estimated difference between groups under the reported analysis. Because the sponsor's analysis is a mixed model for repeated measurements, its contrast is not simply the difference between the two posted group means. The model's full specification and the assumptions it used are not reported in the registry record.

HbA1c is the primary measure named in the record, while fasting plasma glucose and fructosamine are among the secondary measures. Results for a primary endpoint can help organize interpretation because it identifies the main outcome the trial set out to compare. The record does not report a clinical threshold for interpreting the size of the HbA1c change, so the statistical estimates alone do not establish whether a particular difference would be clinically important.

7. Results Posted in the Registry

• Biphasic Insulin Aspart 30: mean -1.13 versus -1.11 on control; difference -0.02 (95% CI -0.38 to 0.34), standardized effect d = -0.01; z-test p = 0.913.

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 in Fasting Plasma Glucose (FPG)

• 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:
  • Biphasic Insulin Aspart 30: mean -4.40 versus -2.00 on control; difference -2.40 (95% CI -6.42 to 1.62), standardized effect d = -0.16; z-test p = 0.242.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biphasic Insulin Aspart 30 and the control. The interval gives the range of effects that remain compatible with the data.

Change in Fructosamine

• 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:
  • Biphasic Insulin Aspart 30: mean -0.04 versus -0.04 on control; difference 0.00 (95% CI -0.01 to 0.01), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Biphasic Insulin Aspart 30 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the description beyond HbA1c, including fasting plasma glucose, fructosamine, target attainment and hypoglycaemia measures. Numeric results are posted for change in fasting plasma glucose and change in fructosamine. The registry lists additional secondary outcomes, but their results are not reported in the registry record. The posted secondary findings should therefore be understood as a partial view of the planned outcome set, rather than a complete account of all secondary measures.

Across the available continuous secondary measures, the pattern is not a uniform extension of the primary result: the fasting plasma glucose estimates show a group contrast with a wide recalculated interval, while the fructosamine group mean changes are the same at the displayed precision. These measures use different scales and have different variability. They are contextual evidence and should not be read as interchangeable replications of the HbA1c result.

The registry does not provide sponsor-reported analyses for these secondary continuous outcomes. Their posted recalculations are unadjusted, and the record does not report how the study handled the possibility of chance findings across multiple secondary outcomes. When many outcomes are examined, some may appear noteworthy by chance alone. Without a reported multiplicity plan and complete results, secondary findings generally carry less confirmatory weight than a prespecified primary outcome.

Secondary outcomes can still help describe what was measured and identify questions for further study. They do not establish that a primary result is confirmed or contradicted, particularly when analyses are unadjusted and some listed outcomes lack posted results. The registry does not report a hierarchy or testing sequence that would support stronger claims from these outcomes.

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

• Change in Fasting Plasma Glucose (FPG)
• Change in Fructosamine
• Number of Subjects Who Achieve HbA1c Below 7% (53 mmol/Mol (American Diabetes Association (ADA) Target )
• Number of Subjects Who Achieve FPG Below or Equal to 7.2 mmol/L (ADA Target)
• Number of Treatment Emergent Hypoglycaemic Episodes Both According to the Novo Nordisk Definition for Hypoglycaemic Episodes (Severe or BG Hypoglycaemia) as Well as According to the ADA definition1 Confirmed Symptomatic
• Number of Treatment Emergent Nocturnal (00:01-05:59 am) Severe or BG Confirmed Symptomatic Hypoglycaemic Episodes

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean change describe?

A mean change is the average difference between measurements at the endpoint and baseline within a group. For this trial, the primary measure is change in HbA1c from week 0 to day 29 of Ramadan. The group means of -1.11 and -1.13 are estimates of average change, not individual participant responses. A group mean can conceal variation among participants, which is why the accompanying uncertainty measures matter. The registry reports least-squares means for the primary outcome; these are model-based means rather than simple arithmetic averages. The model details needed to reproduce them are not reported in the registry record.

Why are the standard errors and standard deviations different?

A standard error describes the uncertainty in an estimated mean. It generally becomes smaller as the amount of information supporting the estimate increases, and it is used to quantify precision. A standard deviation describes how dispersed individual observations are around a mean. It describes variation among observations rather than uncertainty in the mean itself. The primary HbA1c group results are reported with standard errors of 0.13. The secondary continuous outcomes are reported with standard deviations. The measures answer different questions and should not be compared as though they were the same kind of spread.

The unadjusted primary recalculation uses the posted group summaries and an approximate standard deviation derived from the reported standard errors. It is a simple comparison of summary statistics, not a reproduction of the sponsor's repeated-measures model. The registry marks the approximation as approximate. For that reason, the recalculated interval and p-value are useful as a transparent, unadjusted check, but they do not replace the sponsor-reported analysis.

What does the treatment contrast represent?

The sponsor's analysis is described as a mixed model for repeated measurements and reports a treatment contrast. In general, a mixed model for repeated measurements can use observations collected at multiple time points and account for the fact that measurements from the same participant are related. Model-based contrasts estimate a comparison between treatment groups according to the chosen model. The registry does not report the precise time points entered, the covariance structure, covariates, missing-data assumptions or other specification details. It is therefore not possible to determine from the registry record exactly how each modeling choice affected the result.

The reported contrast is 0.02, with a 95% confidence interval from -0.20 to 0.24 and p=0.843. The recalculated unadjusted contrast is -0.02, with a 95% confidence interval from -0.380 to 0.340 and p=0.913. These estimates differ because the sponsor analysis and the recalculation use different methods and summaries. The record does not give enough information to attribute the differences to a particular model feature.

How should a confidence interval be read?

In general, a confidence interval describes the range of estimates reasonably compatible with the data and the analysis assumptions at a stated confidence level. It expresses uncertainty about an estimated contrast; it is not a guarantee that the true value lies inside the particular interval. A narrower interval indicates greater precision than a wider interval, for the same measure and method. Both the sponsor-reported and recalculated primary intervals include zero, meaning each is compatible with no group contrast as well as with contrasts in either direction. The endpoints also show how large a range of differences remains compatible with each analysis.

Confidence intervals do not by themselves determine clinical importance. That interpretation requires context, such as a prespecified threshold for a meaningful difference. Such a threshold is not reported in the registry record. Likewise, the fact that an interval includes zero does not establish equivalence: an equivalence assessment requires an appropriate design and a defined margin.

What do the p-values say?

A p-value is calculated under a statistical model and a null hypothesis, and describes how unusual data at least as incompatible with that null would be under those assumptions. It is not a measure of the size of an effect, nor does it state the probability that the treatments are the same. The sponsor-reported p-value and the recalculated unadjusted p-value come from different analyses. The latter is not adjusted for repeated measurements or other model features, and the record does not describe a multiplicity adjustment. Their interpretation should retain that distinction.

Why can over-dispersion matter?

In general, over-dispersion occurs when the variability in observed data is greater than a statistical model expects. When that happens, standard errors can be understated if the model does not accommodate the extra variation, making confidence intervals too narrow and tests too optimistic. This is a general statistical consideration, not a reported finding about this trial. The primary endpoint is continuous, and the registry does not report an over-dispersion assessment. For count outcomes such as episodes, the appropriate distributional assumptions would depend on the event data and model; those detailed analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor-reported primary contrast is 0.02, with a 95% confidence interval from -0.20 to 0.24. The unadjusted recalculation from the posted group summaries is -0.02, with a 95% confidence interval from -0.380 to 0.340. Both intervals include zero, and each allows for differences in either direction. The sponsor-reported interval is narrower than the recalculated interval, but the two intervals come from different methods and should not be interpreted as if they were interchangeable estimates.

In general, a confidence interval conveys precision as well as the range of values compatible with the data and analysis. A narrower interval indicates a more precise estimate under the method used; a wider interval indicates greater uncertainty. The recalculation is unadjusted and uses an approximate standard deviation inferred from the primary outcome's standard errors. The sponsor result comes from a mixed model for repeated measurements. Since the registry does not report the full model specification, the source of the difference in interval width cannot be determined from the record.

The intervals are not evidence that the regimens are equivalent. The record does not report an equivalence margin or a non-inferiority margin. Without such a margin, the confidence limits cannot be judged against a prespecified acceptable difference. The estimates therefore describe the observed statistical precision, not whether any possible difference is clinically unimportant.

Precision also depends on the analysis population and available measurements. The registry says that the analyzed number represents participants who contributed to the primary analysis, but does not report a detailed account of missing primary outcome data. That limits assessment of how missingness may affect the estimates and their precision.

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 expressed as participants per arm, not as total event counts. They are illustrations based on the observed effect, rather than the trial's own original design calculation. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation and an effect to detect equal to the stated fraction of the observed effect. The registry's original design assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding planning number for a 90% chance. Power is a property of a planned study under assumptions, not a measure of how likely the observed result is to be true.

The planning rows express effects as 100%, 75% and 50% of the observed effect. The smaller the effect being targeted, the more participants are needed to distinguish it from random variation under the same assumptions. These calculations use the observed contrast as their starting point; a very small observed contrast can therefore lead to very large planning illustrations. The figures should be read as sensitivity examples, not as recommendations for a future study or as evidence about what sample size the sponsor intended.

These values are not observed power. Observed power calculated from the result would not add useful information beyond the estimate and its confidence interval. The confidence interval is the more direct description of how precisely the trial estimated the treatment contrast.

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 = -0.020; pooled standard deviation σ = 1.439.
2. n = 2 × (1.96 + 0.842)² × 1.439² / -0.020² = 81,258.0, rounded up to 81,258 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 <- -0.0199999999999998                      # observed difference in means
sigma <- 1.43894508684764                     # 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(2648217)
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 = 81,258 (80% power), 108,782 (90% power)
 75% of observed effect: n per arm = 144,459 (80% power), 193,390 (90% power)
 50% of observed effect: n per arm = 325,032 (80% power), 435,126 (90% power)
power.t.test: 81259 
Simulated power at n = 81,258 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 registry reports the sponsor's primary analysis as a mixed model for repeated measurements. It gives a treatment contrast of 0.02, a 95% confidence interval from -0.20 to 0.24, and p=0.843. This is the sponsor-reported analysis and is distinct from the simple unadjusted recalculation based on posted group summaries.

The recalculation gives a contrast of -0.02, a 95% confidence interval from -0.380 to 0.340, and an unadjusted p-value of 0.913. The recalculated result is not intended to substitute for the sponsor's model. The signs differ, and the estimates and intervals are not identical. Both point estimates are close to zero, and both confidence intervals include zero. The record does not provide the model details needed to explain the numerical differences.

The record does not flag a discrepancy between the sponsor analysis and the posted outcome information. The sponsor's analysis should be interpreted according to the method it reports, while the recalculation should be read as a separate unadjusted summary-statistic comparison. Neither result establishes equivalence, and the registry does not report a margin against which equivalence or non-inferiority could be assessed.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and lists secondary outcomes, but a strategy for controlling multiplicity is not reported in the registry record. Multiplicity arises when several outcomes, comparisons or analyses are considered: the more opportunities there are to find a small p-value, the greater the chance of at least one chance finding. Common approaches include prespecifying a hierarchy or adjusting the testing threshold, but the record does not say that either approach was used. The posted unadjusted secondary comparisons should therefore be treated as exploratory evidence rather than as a collection of confirmatory tests.

The registry does not report the original statistical analysis plan, interim analyses, or a detailed account of missing data. The primary outcome description says that the analyzed number counts participants who contributed to the analysis. It does not explain why some enrolled participants are not included in the analyzed counts, how many measurements were missing at each time point, or how missing observations were handled by the repeated-measures model. Missing-data assumptions can affect model estimates and their uncertainty, so these omissions limit independent assessment.

The record also does not fully define analysis populations, such as whether the primary analysis followed an intention-to-treat principle or a per-protocol approach. It does not describe exclusions after randomization or give reasons for any exclusions. Those details matter because comparisons can be affected if the analyzed participants differ systematically from those randomized.

The registry's statement that the analyzed numbers count participants who contributed to the analysis is useful, but it is not a full missing-data or population definition. In the absence of further reporting, the estimates should be interpreted as applying to the analyses and participants described in the record, without assuming a particular missing-data method or analysis population.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: myocardial infarction (1.5%), hypoglycaemia (1.5%), endometrial adenocarcinoma (0.8%), fall (0.8%), intervertebral disc protrusion (0.8%).

For serious adverse events, the registry reports 5 affected participants among 130 at risk in the insulin degludec/insulin aspart group and 3 among 132 at risk in the biphasic insulin aspart 30 group. For other adverse events, it reports 54 among 130 and 47 among 132, respectively. These are participant counts, not counts of all event episodes; the record does not provide enough detail to determine whether an individual could have had more than one event.

The listed serious adverse event terms include myocardial infarction and hypoglycaemia at 1.5% each, and endometrial adenocarcinoma, fall, intervertebral disc protrusion and lumbar spinal stenosis at 0.8% each. The record does not specify in this summary how these terms were distributed by treatment group. Deaths are not reported in the registry record; a missing entry should not be interpreted as zero deaths.

These figures are descriptive. The registry does not provide a statistical comparison of serious adverse events, and the counts alone do not establish a difference in safety between groups. The number of participants at risk and the scope of the adverse event reporting should be considered when reading the counts.

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

The primary outcome estimates show mean HbA1c changes of -1.11 with insulin degludec/insulin aspart and -1.13 with biphasic insulin aspart 30 from week 0 to the end of Ramadan. The sponsor-reported treatment contrast is 0.02, with a 95% confidence interval from -0.20 to 0.24. The unadjusted recalculation is -0.02, with a 95% confidence interval from -0.380 to 0.340. These results describe estimates near zero, but the intervals retain uncertainty about the direction and size of a possible difference.

The result does not demonstrate that the regimens are equivalent. An interval that includes zero does not rule out differences, and equivalence requires a prespecified margin and a suitable analysis. Neither an equivalence margin nor a non-inferiority margin is reported in the registry record. The record also does not report a threshold for deciding what size of HbA1c difference would be clinically important. Statistical uncertainty and clinical importance are related questions, but they are not the same.

The findings apply to the measured outcome and timeframe: change in HbA1c through day 29 of Ramadan. They do not, by themselves, describe outcomes beyond that timeframe or establish results for every listed secondary outcome. The available secondary estimates are unadjusted, and results for several listed outcomes are not reported in the registry record.

The trial is described as randomized, which supports a comparative design, but the registry record does not provide all details needed to assess allocation procedures, missing data or the analysis population. The estimates should be read with those reporting limits in mind. They describe the posted results; they are not medical advice or a basis for individual treatment decisions.

18. Why This Trial Matters Statistically

This trial offers a focused example of why a group estimate, its uncertainty and the analysis method need to be read together. The posted group mean changes in HbA1c are close, and the sponsor-reported repeated-measures contrast is also near zero. Yet the confidence intervals remain essential: they show that the estimate is not known with unlimited precision and that a range of differences remains compatible with the data.

The record also permits comparison between a sponsor-reported model analysis and an unadjusted recalculation from summary statistics. Those analyses are not interchangeable. The model uses repeated measurements, while the recalculation works from posted group summaries and an approximate standard deviation. Their differing estimates and intervals demonstrate why an independent recalculation is a check on interpretation, not a replacement for the trial's stated model.

Planning illustrations based on an observed effect require particular care. When a small observed contrast is used as the target effect, the resulting participant requirements can become large. Such figures describe hypothetical planning under stated assumptions; they are not observed power and do not tell readers what the original trial was designed to detect. The original design assumptions are not reported in the registry record.

Finally, secondary measures and safety counts add context but have limits when multiplicity, missing data and analysis populations are not fully described. A statistically careful reading distinguishes the primary estimate from secondary exploratory evidence, and distinguishes descriptive adverse event counts from comparative safety conclusions. That discipline keeps the interpretation within what the registry record actually reports.

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 reporting limitations are specific to interpreting this trial's results. The registry identifies the primary analysis as a mixed model for repeated measurements but does not report its full specification. Covariates, covariance structure, time-point handling and missing-data assumptions are not reported in the registry record. This makes it difficult to reproduce the sponsor's treatment contrast or to explain precisely why it differs from the unadjusted recalculation.

The primary analysis counts participants who contributed to the analysis, but the record does not provide a detailed participant flow, reasons for missing data or the precise analysis population. The original sample-size justification and the trial's own target effect are also not reported. Consequently, the planning illustrations based on the observed effect should not be mistaken for the original design calculation.

Multiplicity handling is not reported, and numeric results are not reported in the registry record for all listed secondary outcomes. This limits the strength of conclusions that can be drawn from the secondary outcome set as a whole. The available recalculated secondary comparisons are unadjusted and should be interpreted with that limitation.

The registry describes the trial as open-label and does not report the allocation ratio, randomization method or allocation concealment. It also does not report a clinical threshold for interpreting the primary contrast or an equivalence or non-inferiority margin. These omissions constrain judgments about clinical meaning and the robustness of the comparison.

Safety information is presented as affected participant counts and selected serious event terms. Deaths are not reported in the registry record, and the listed terms are not assigned to treatment groups in the registry record. The reported counts should therefore remain descriptive rather than being used to infer a comparative safety effect.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparing Efficacy and Safety of Insulin Degludec/Insulin Aspart Twice Daily and Biphasic Insulin Aspart Twice Daily in Subjects With Type 2 Diabetes Mellitus Before, During and After Ramadan — NCT02648217.
• Registry record last updated 2018-09-11; status last verified 2017-12.
• Results first posted 2018-09-11.
• 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

This completed phase 3 trial randomized participants with type 2 diabetes mellitus to twice-daily insulin degludec/insulin aspart or biphasic insulin aspart. The record describes an open-label, parallel-group design and an enrollment of 263, with the trial conducted in Africa and Asia.

The primary outcome was change in HbA1c from week 0 to day 29 of Ramadan. The sponsor-reported mixed-model contrast was 0.02, with a 95% confidence interval from -0.20 to 0.24 and p=0.843. The unadjusted recalculation was -0.02, with a 95% confidence interval from -0.380 to 0.340 and p=0.913. Both estimates are near zero, but neither establishes equivalence.

The registry includes selected secondary outcome and adverse event information, while some listed results and important analysis details are not reported in the registry record. The findings should be understood within the stated outcome period and these reporting limits.