Research Study to Compare a New Medicine "Fast-acting Insulin Aspart" to Another Medicine "Insulin Aspart" in Chinese People With Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Research Study to Compare a New Medicine "Fast-acting Insulin Aspart" to Another Medicine "Insulin Aspart" in Chinese People With Diabetes (NCT04588259), a randomized phase 3 study. The primary outcome is Change From Baseline in Glycosylated Haemoglobin (HbA1c) (Percentage [%]).

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase 3 trial sponsored by Novo Nordisk A/S. The registry lists quadruple masking, meaning the record classifies the study as masked across four roles or parties; it does not name those roles in the information available. The listed enrollment was 331. The registry status is completed, and the listed study dates run from 2020-10-09 to primary completion on 2022-07-05.

The two treatment groups received faster aspart or NovoRapid, each alongside insulin degludec and with or without metformin. The brief summary describes a study lasting about 7 months (30 weeks), with clinic visits, phone contacts, blood sampling, and participant diaries. Some visits involved fasting and a meal test. These details describe the study procedures, but the primary endpoint was assessed at week 16, not at the end of the described study period.

The primary outcome analysis used the full analysis set, which the record defines as all randomized participants, with the analysed number determined by contribution to the analysis. The arm summaries report 143 participants for faster aspart and 145 for NovoRapid for the primary endpoint. The registry lists 29 outcome measures and 2 analyses overall, and 27 posted secondary outcomes. The original sample-size calculation, its assumptions, and the planned analysis details beyond the reported methods are not reported in the registry record.

The design supports a randomized comparison of the assigned regimens, but the available summary cannot establish whether all features of treatment delivery, follow-up, or missing-data handling were balanced or how they were implemented. Those details 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: The trial included an 8-week run-in period and a 16-week treatment period. During the run-in period, participants received NovoRapid both in combination with insulin degludec with or without metformin primarily for optimisation of the basal insulin treatment. Participants were then randomised 1:1 to receive either 'Faster aspart + insulin degludec with or without metformin' or 'NovoRapid + insulin degludec with or without metformin' during the treatment period.

Run-in period

Reasons for not completing this period:

Treatment period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) which included all randomised participants. Number of participants analysed = Number of participants 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: Full analysis set (FAS) which included all randomised participants.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Glycosylated Haemoglobin (HbA1c) (Percentage [%]), measured over Baseline (week 0), week 16.

The primary endpoint is the mean change from baseline in glycosylated haemoglobin, or HbA1c, measured as a percentage. It compares the baseline value at week 0 with the value assessed at week 16 after randomization. The registry describes the result as based on the last in-trial value, including the last available measurement during the in-trial period.

HbA1c is used as a measure of longer-term blood glucose exposure. In general, it provides a different perspective from a single glucose measurement, which reflects glucose at a particular time. A change-from-baseline outcome focuses on how the measured value shifts over follow-up, while comparing the treatment groups asks whether their average changes differ.

The reported arm means are changes in HbA1c, so negative values represent a decrease from baseline in the measure. The primary comparison is the treatment difference between groups, not whether either group changed on its own. The registry identifies the sponsor's analysis as a non-inferiority analysis. That label describes the intended type of comparison, but assessing non-inferiority requires a prespecified margin. The margin is not reported in the registry record, so the numerical estimate and confidence interval can be described, but the criterion cannot be checked from the record alone.

7. Results Posted in the Registry

• NovoRapid: mean -0.54 versus -0.57 on control; difference 0.03 (95% CI -0.13 to 0.19), standardized effect d = 0.04; z-test p = 0.709.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline 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:
  • NovoRapid: mean 0.20 versus 0.39 on control; difference -0.19 (95% CI -0.72 to 0.34), standardized effect d = -0.08; z-test p = 0.486.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NovoRapid and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in 7-9-7-point Self-measured Plasma Glucose (SMPG) for Mean of the 7-9-7-point Profile

• 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:
  • NovoRapid: mean -0.76 versus -0.73 on control; difference -0.03 (95% CI -0.42 to 0.36), standardized effect d = -0.02; z-test p = 0.879.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NovoRapid and the control. The interval gives the range of effects that remain compatible with the data.

Insulin Dose (Units/Day): Total Basal

• 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:
  • NovoRapid: mean 27.21 versus 27.01 on control; difference 0.20 (95% CI -3.00 to 3.40), standardized effect d = 0.01; z-test p = 0.902.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NovoRapid and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes, including post-meal glucose measures, fasting plasma glucose, self-measured glucose profiles, insulin dose, and achievement of an HbA1c threshold. The numerical secondary summaries include comparisons of fasting plasma glucose, the mean self-measured glucose profile, and total basal insulin dose. Their estimates are generally close to zero relative to their reported variability, and the recalculated confidence intervals include zero.

This overall pattern is compatible with the primary comparison's lack of a clear separation between the group estimates in the posted summaries. It does not independently confirm the primary result, and it should not be read as proof that every secondary outcome is equivalent between treatments. Each outcome measures a different aspect of glucose or treatment, and its estimate has its own uncertainty.

Unadjusted secondary results carry less weight when many outcomes are examined because the chance of at least one apparently notable result can increase across multiple comparisons. A prespecified hierarchy or adjustment can address that concern, but a multiplicity strategy is not reported in the registry record. The secondary outcomes therefore provide contextual, largely exploratory information rather than a separate confirmatory basis for the trial's conclusion. Detailed numerical interpretations for individual secondary outcomes belong with their corresponding posted statistics.

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

• Change From Baseline in 30-minutes, 1-hour, 2-hour and 3-hour Post Prandial Glucose (PPG) Increment (Meal Test)
• Change From Baseline in 30-minutes, 1-hour, 2-hour and 3-hour PPG (Meal Test)
• Change From Baseline in Fasting Plasma Glucose (FPG)
• Change From Baseline in 7-9-7-point Self-measured Plasma Glucose (SMPG) for Mean of the 7-9-7-point Profile
• Change From Baseline in 7-9-7-point SMPG for 1-hour PPG (Mean, Breakfast, Lunch, Main Evening Meal)
• Change From Baseline in 7-9-7-point SMPG for PPG Increment (Mean, Breakfast, Lunch, Main Evening Meal)
• Change From Baseline in 7-9-7-point SMPG for Fluctuation in 7-9-7-point Profile: Ratio to Baseline
• Number of Participants Who Achieved HbA1c Less Than (<) 7.0 (Percent [%]) (Yes/No)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean change describe?

For a continuous outcome such as HbA1c, the mean change summarizes the average difference between a participant's follow-up and baseline measurements within a group. A negative mean change indicates an average reduction in the measured value from baseline; a positive value indicates an average increase. The treatment comparison asks how the group averages differ, rather than treating a within-group change as proof of a treatment effect.

The registry reports a standard deviation for each arm. In general, a standard deviation describes how widely individual measurements vary around the group mean. It is not the same as the standard error, which describes uncertainty in an estimated mean. Greater variability can make a group mean or a between-group contrast less precise, even when the number analysed is unchanged.

How should the treatment difference be read?

A treatment difference is an estimate of the contrast between the groups under a specified analysis. Its sign depends on the order used to subtract one treatment group from the other. The registry reports the sponsor's mixed models treatment difference as -0.05, while the unadjusted recalculation from the group summaries is 0.03. The registry does not give enough detail to attribute the difference between those estimates to a particular model feature. The sponsor's result is the analysis explicitly reported for the primary endpoint; the recalculation is not a substitute for it.

A confidence interval gives a range of values compatible with the data and the assumptions of the analysis at the stated confidence level. In general, a wider interval indicates less precision, while a narrower interval indicates greater precision. An interval that crosses zero is consistent with a range of possible treatment differences in both directions. It is not proof that the true difference is zero, nor does it determine whether a non-inferiority criterion is met.

A p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the model assumptions held. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. For a non-inferiority analysis, the key comparison is generally against a prespecified margin, not only against zero. The margin is not reported in the registry record, so the non-inferiority decision rule cannot be reconstructed.

Why use a mixed models analysis?

In general, mixed models can represent repeated or otherwise correlated observations and can include fixed effects for treatment and other model terms, along with participant-level structure where appropriate. This can allow an analysis to use available measurements while accounting for their dependence. The registry names the sponsor's method as Mixed Models Analysis, but does not report the model formula, covariance structure, included covariates, missing-data assumptions, or other implementation details. Those features should not be inferred from the method label alone.

The sponsor's primary result and the summary-statistic recalculation answer related but not necessarily identical statistical questions. The recalculation uses the posted arm means, standard deviations, and analysed counts to form an unadjusted comparison. It does not reproduce an adjusted or repeated-measures model. The recalculation's confidence interval and p-value should therefore be treated as descriptive cross-checks, not as a replacement for the registry-reported analysis.

What does over-dispersion mean in general?

For count outcomes, over-dispersion occurs when observed variability exceeds what a simple count model assumes. It can make standard errors too small if ignored. This primary endpoint is continuous and is summarized with means and standard deviations; over-dispersion is not a specific reported feature of the primary analysis. The concept is relevant generally, but no over-dispersion assessment is reported in the registry record.

What can the planning illustrations tell us?

The sample-size planning illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They vary the effect to detect as a stated fraction of the observed effect. For continuous outcomes, the displayed figures are participants per arm. They are hypothetical planning illustrations based on observed effects, not the original design calculation. The original sample-size assumptions are not reported in the registry record, and the illustrations are not observed power.

Power is the probability, under specified assumptions, that a planned analysis will reject its null hypothesis if the stated effect is true. The 80% and 90% columns describe different target probabilities of detecting the assumed effect under the planning model. Smaller effects generally require more participants to detect, all else held constant. These illustrations do not show the probability that the trial's result is correct and do not change the interpretation of the observed confidence interval.

What remains unknown?

The registry does not report the planned sample-size justification, a full statistical analysis plan, an interim-analysis plan, the primary non-inferiority margin, a multiplicity adjustment strategy, or detailed missing-data procedures. These omissions limit independent assessment of the confirmatory framework. The analysis population is described as the full analysis set, but further details about participant flow and the handling of unavailable measurements are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is -0.05, with a 95% confidence interval from -0.19 to 0.09. This interval includes zero and spans estimates in both directions. It therefore does not isolate a single precise treatment difference. The interval is also the key indicator of statistical precision: it conveys more about the range of values compatible with the model than the point estimate alone.

The unadjusted recalculation gives a mean difference of 0.03, with a confidence interval from -0.127 to 0.187. It likewise includes zero and permits effects in either direction. The recalculated interval comes from posted summary statistics and does not reproduce the sponsor's mixed models analysis. The two intervals should not be treated as interchangeable estimates from the same method.

Precision and clinical importance are different questions. A confidence interval can be statistically compatible with no difference while still allowing effects that might matter in context; deciding what matters requires a clinical threshold that is not reported in the registry record. For non-inferiority, the interval must be assessed relative to the prespecified non-inferiority margin. Because that margin is not reported in the registry record, the interval alone cannot establish whether the criterion was satisfied.

The uncertainty also matters for interpreting the secondary outcomes. Their recalculated intervals reflect uncertainty around each separate comparison, and unadjusted analyses do not account for the possibility of chance findings across multiple outcomes. The registry record does not report a multiplicity plan. Thus the precision of an individual estimate should not be confused with the strength of the overall evidence across all outcomes.

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 illustrations are for continuous outcomes, so the figures are participants per arm, not total events. They use the observed effect as a starting point and show planning scenarios for detecting 100% of that effect, 75% of the observed effect, and 50% of the observed effect. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation.

The 80% power column represents a planning target in which the specified effect would be detected in 80% of repetitions under the model assumptions. The 90% power column uses a higher target probability of detection and therefore generally requires more participants for the same assumed effect. These are hypothetical planning quantities, not results from the trial itself.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. The displayed figures can illustrate how sensitive a design may be to the effect size chosen, but they do not reveal what effect the original investigators planned to detect. The original trial's design assumptions and sample-size justification are not reported in the registry record. This is not observed power: observed power is not an informative substitute for the uncertainty represented by the actual estimate and confidence interval.

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 = 0.030; pooled standard deviation σ = 0.682.
2. n = 2 × (1.96 + 0.842)² × 0.682² / 0.030² = 8,117.1, rounded up to 8,118 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 <- 0.0299999999999999                      # observed difference in means
sigma <- 0.682184377185175                     # 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(4588259)
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 = 8,118 (80% power), 10,867 (90% power)
 75% of observed effect: n per arm = 14,431 (80% power), 19,319 (90% power)
 50% of observed effect: n per arm = 32,469 (80% power), 43,466 (90% power)
power.t.test: 8118 
Simulated power at n = 8,118 per arm: 0.803 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reported a Mixed Models Analysis for the primary endpoint, with a treatment difference of -0.05, a 95% confidence interval from -0.19 to 0.09, and p = 0.510. The registry labels this analysis as non-inferiority. It is the sponsor's reported primary analysis and should be distinguished from the simple recalculation based on posted arm means and standard deviations.

The recalculation estimates a mean difference of 0.03, with a confidence interval from -0.127 to 0.187 and an unadjusted p-value of 0.709. It is not a reproduction of the mixed models analysis, and the record does not give enough methodological detail to explain why the point estimates differ. The discrepancy flag is false, but that does not make the two methods identical or remove the need to identify which analysis is being interpreted.

The sponsor's non-inferiority designation cannot be independently assessed without the non-inferiority margin and the relevant analysis details. The margin is not reported in the registry record. The sponsor-reported estimate and interval should therefore be presented as the primary reported analysis, with the recalculation clearly identified as an unadjusted supplementary comparison rather than a competing primary result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 29 outcome measures, 27 posted secondary outcomes, and 2 analyses overall. When numerous outcomes or comparisons are examined, multiplicity becomes relevant: without a prespecified strategy, chance findings can be overrepresented among results that appear noteworthy. Possible approaches include a hierarchy of hypotheses or an adjustment to control error across comparisons. The registry record does not report a multiplicity strategy, so it is not possible to tell whether or how the secondary analyses were adjusted or prioritized.

The primary outcome is identified, and the sponsor's analysis is labeled non-inferiority, but the non-inferiority margin is not reported in the registry record. The full analysis plan, including the exact model specification and decision rules, is also not reported. This limits independent evaluation of whether the reported analysis followed a prespecified plan and how its result was intended to support a non-inferiority conclusion.

The primary analysis population is the full analysis set, which the record defines as all randomized participants. The record states that the number analysed is the number contributing to the analysis. It does not report detailed participant flow, reasons for missing outcome values, the extent or pattern of missingness, or the method used to handle missing data. The description that the endpoint uses the last available in-trial measurement does not by itself establish how missing values were treated or what assumptions were made about them.

The original sample-size rationale and any interim-analysis plan are not reported in the registry record. These omissions do not erase the observed estimates, but they make it harder to assess the original design's intended precision and the confirmatory framework. Interpretations should remain tied to the reported estimates and their uncertainty, without assuming unreported procedures.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina unstable (0.7%), arteriosclerosis coronary artery (0.7%), bronchitis (0.7%), carpal tunnel syndrome (0.7%), cerebral infarction (0.7%).

The registry separates serious adverse events during the NovoRapid run-in period from events during the faster aspart and NovoRapid treatment periods. For serious adverse events, the record lists 9 affected participants among 331 at risk during the run-in period, 10 among 150 at risk for faster aspart, and 7 among 150 at risk for NovoRapid. The listed death count is 0 in each period. These are recorded counts and denominators for the stated periods; they should not be combined into a single comparison because the run-in period is distinct from the treatment periods.

For other adverse events, the record lists 32 affected participants among 331 at risk during run-in, 55 among 150 at risk for faster aspart, and 40 among 150 at risk for NovoRapid. The serious-event terms listed include angina unstable, arteriosclerosis coronary artery, bronchitis, carpal tunnel syndrome, cerebral infarction, and diabetic foot, each reported as 0.7%.

These summaries are descriptive. They do not establish whether an event was caused by a treatment, and the registry record does not provide enough detail to assess event timing, exposure-adjusted rates, or the clinical context of individual events. Counts should be read with their stated periods and denominators, not as proof of comparative safety.

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

The posted primary results show similar average changes in HbA1c in the two treatment groups, with a sponsor-reported treatment difference close to zero and a confidence interval that includes zero. The unadjusted recalculation also has a confidence interval spanning zero. These findings describe the estimates and their uncertainty; they do not prove that the treatments are identical or that no meaningful difference exists.

The record identifies the sponsor analysis as non-inferiority, but the margin required to judge that claim is not reported in the registry record. Without the margin, readers cannot determine whether the confidence interval satisfies the stated non-inferiority criterion. The reported label should therefore not be mistaken for an independently verifiable conclusion based solely on the available summary.

The results concern the studied regimens: faster aspart or NovoRapid, each with insulin degludec and with or without metformin, in the described adult diabetes population. They do not establish effects in populations or treatment settings not described in the registry. The reported outcome is HbA1c change at week 16, not every aspect of glucose control, longer-term outcomes, or all possible harms.

Secondary measures offer additional context but are subject to their own uncertainty, and the registry record does not report how multiplicity was handled. Safety counts are likewise descriptive and do not establish causation. No medical decision should be based on these statistics alone; the record is a summary of one trial, not a complete assessment of an individual's circumstances or the broader evidence.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison cannot be reduced to asking whether a p-value crosses a threshold. The estimate, confidence interval, analysis method, and question being tested all matter. The sponsor reports a mixed models non-inferiority analysis, while a summary-statistic recalculation gives a different point estimate. Distinguishing those analyses prevents a simple unadjusted calculation from being mistaken for the prespecified or sponsor-reported model.

It also shows that a non-inferiority label is not enough to evaluate a non-inferiority claim. The margin defines how much difference the design would accept, and it is not reported in the registry record. The confidence interval therefore cannot be judged against that criterion using the record alone.

The secondary outcomes and safety counts illustrate further statistical issues. Multiple unadjusted comparisons require caution, and adverse-event counts need to be interpreted in the context of their periods and denominators rather than as causal treatment effects. Across these elements, transparent reporting of the analysis plan, missing-data handling, multiplicity approach, and non-inferiority margin would make independent assessment more complete.

The record remains useful because it identifies the randomized comparison, primary endpoint, sponsor-reported estimate, and available uncertainty. Its limits are also instructive: numerical results can be reported precisely while important design and analysis details remain unavailable. Statistical interpretation depends on both what the estimates show and what information is needed to evaluate the intended claim.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary analysis is labeled non-inferiority, but the margin is not reported in the registry record. This is a central limitation for interpreting whether the sponsor's analysis meets its intended criterion. The registry also does not report the full model specification, the non-inferiority decision rule, or enough detail to explain the difference between the sponsor's mixed models estimate and the unadjusted recalculation.

The original sample-size calculation and its assumptions are not reported, so the planning illustrations based on observed effects cannot be treated as evidence about the trial's intended precision. The registry does not report an interim-analysis plan or a multiplicity strategy, despite listing numerous outcome measures. The primary results can be read, but the confirmatory status of the secondary comparisons cannot be established from the record alone.

The full analysis set is defined as all randomized participants, but detailed participant flow, reasons for missing outcomes, and missing-data methods are not reported. The endpoint description refers to the last available in-trial measurement, without enough information to establish how unavailable measurements were handled or what assumptions underlie the analysis.

The safety summary provides affected-participant counts and at-risk denominators by period, but does not establish causality or provide the context needed for a comprehensive comparison. The run-in period is reported separately from treatment periods. The registry's summaries should therefore be interpreted as descriptive trial-record information rather than a complete account of efficacy, safety, or generalizability.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Research Study to Compare a New Medicine "Fast-acting Insulin Aspart" to Another Medicine "Insulin Aspart" in Chinese People With Diabetes — NCT04588259.
• Registry record last updated 2025-12-04; status last verified 2025-11.
• Results first posted 2024-03-20.
• 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, parallel-group phase 3 trial of faster aspart versus NovoRapid, with both regimens used alongside insulin degludec and with or without metformin. It lists quadruple masking and enrollment of 331. The primary endpoint is change from baseline in HbA1c at week 16.

The sponsor's Mixed Models Analysis reports a treatment difference of -0.05, with a 95% confidence interval from -0.19 to 0.09 and p = 0.510, and is designated as non-inferiority. The non-inferiority margin is not reported in the registry record. An unadjusted recalculation from the arm summaries gives a mean difference of 0.03, with a confidence interval from -0.127 to 0.187.

The record also lists secondary glucose and insulin-dose outcomes and descriptive adverse-event counts. Details needed to fully evaluate multiplicity, missing-data handling, the original sample-size rationale, and the non-inferiority criterion are not reported in the registry record.