Comparison of NN1250 With Insulin Glargine in Subjects With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of NN1250 With Insulin Glargine in Subjects With Type 2 Diabetes (NCT01068678), a randomized phase 3 study. The primary outcome is Change in Glycosylated Haemoglobin (HbA1c).

2. Clinical Question

3. Trial Design

This was a Phase 3, randomised, parallel-group trial with no masking recorded in the registry. The study compared insulin degludec, labelled IDeg 3TW, with insulin glargine, labelled IGlar OD, in subjects with type 2 diabetes receiving metformin alone or metformin with an oral anti-diabetic drug and qualifying for intensified treatment. The registry identifies Novo Nordisk A/S as the sponsor. The recorded enrollment was 460.

The record gives a start of 2010-02, a primary completion of 2010-11, and a completed status. Its brief summary describes the trial as conducted in Africa, Asia, Europe, and North America. These dates and status describe the registry entry; they do not by themselves supply details of recruitment timing, follow-up after the primary endpoint, or how the trial was operationally managed.

The primary endpoint was change from baseline in HbA1c after Week 26. The primary outcome population was the Full analysis set, defined in the record as including all randomised subjects. Missing data for that analysis were imputed using last observation carried forward (LOCF). The record notes that one subject was randomised despite being a screening failure. The posted arm counts for the primary outcome are 229 for IDeg 3TW and 230 for IGlar OD. The secondary outcome listed is change in body weight at Week 26; its arm counts are 227 and 229.

The registry does not report details of the randomisation sequence, allocation concealment, masking procedures beyond the entry of none, treatment adherence, or how outcomes were collected. It also does not report the trial's original sample-size justification or original statistical analysis plan. Those omissions mean that the summary can describe the registered design and posted results, but cannot establish how every design choice was made or implemented.

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: The Full analysis set (FAS) included all randomised subjects and missing data is imputed using last observation carried forward (LOCF).1 subject was randomised despite being a screening failure.

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)- included all randomised subjects. 1 subject was randomised despite being a screening failure

6. Primary Endpoint

The registry lists the primary outcome as Change in Glycosylated Haemoglobin (HbA1c), measured over Week 26.

The primary endpoint is change from baseline in glycosylated haemoglobin (HbA1c) after Week 26, measured as a percentage of glycosylated haemoglobin. The reported summary is a mean change for each treatment arm, with a standard deviation describing the spread of individual changes around each arm's mean. The treatment comparison is expressed as a mean difference between arms.

HbA1c is commonly used in diabetes trials because it reflects glycaemic status over a period of time rather than a single measurement at one moment. As a continuous outcome, it allows the analysis to describe both the direction and average size of change and the variation among participants. A change-from-baseline endpoint also places the comparison in terms of how measurements shifted during the trial, rather than only comparing the final values.

The endpoint's timing matters: the posted primary measure concerns Week 26, so it represents the specified follow-up point and not a longer-term pattern. The registry's description says that missing values in the Full analysis set were imputed using last observation carried forward. That method carries the last available observation forward for a participant with missing data; it can simplify inclusion of incomplete follow-up but relies on an assumption about what an unobserved later value represents. Whether that assumption is appropriate cannot be determined from the posted summary alone.

HbA1c is one outcome among several relevant clinical measures. The registry lists change in body weight as a secondary endpoint. Considering the primary endpoint separately from secondary outcomes helps preserve the distinction between the trial's designated main question and additional measures.

7. Results Posted in the Registry

• IGlar OD: mean -1.40 versus -1.00 on control; difference -0.40 (95% CI -0.59 to -0.21), standardized effect d = -0.40; z-test p = <0.001.

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 Body Weight

• 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:
  • IGlar OD: mean 1.00 versus 0.80 on control; difference 0.20 (95% CI -0.47 to 0.87), standardized effect d = 0.05; z-test p = 0.559.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between IGlar OD and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint, change in body weight at Week 26, alongside the primary HbA1c endpoint. The secondary outcome offers a complementary measure rather than a substitute for the primary question. Considering the outcomes together gives a broader description of the posted results, but each endpoint addresses a different aspect of change and should be interpreted on its own scale.

The overall pattern is that the primary HbA1c comparison is more statistically distinct in the unadjusted results, whereas the secondary body-weight comparison is uncertain and its interval includes zero. This does not create a contradiction: different outcomes can show different patterns, and their estimates have different variability and precision. Nor does a secondary result explain the primary result. The endpoint summaries do not establish a causal mechanism linking the measures.

Secondary analyses generally carry less confirmatory weight than a prespecified primary analysis, especially when several outcomes or comparisons may be examined. Testing multiple hypotheses increases the chance that at least one result appears statistically notable by chance. Adjustment procedures or a hierarchy of tests can address aspects of this issue, but the registry record does not report a multiplicity plan. The posted secondary p-value is unadjusted, and it should not be interpreted as if a correction had been applied.

Only one secondary outcome is listed in the record, and no secondary analyses are reported in the registry entry. That does not establish what was examined in the full study documentation or whether other outcomes were measured; those details are not reported in the registry record. The posted secondary finding is best treated as supportive descriptive information rather than a separate definitive conclusion. Its weight also depends on the broader analysis plan, completeness of outcome reporting, and the degree to which the endpoint was prespecified, details that are not fully available in the record.

In practice, the secondary result can inform how the primary contrast sits alongside another measured outcome, while retaining the distinction between confirmatory and exploratory evidence. Neither the presence nor absence of a statistically notable secondary finding should be used to override the primary analysis. The registry's limited reporting on multiplicity and secondary analyses means that the full inferential context cannot be reconstructed from the posted results alone.

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

• Change in Body Weight

9. Statistical Interpretation

10. Statistical Methods Explained

The posted continuous outcomes are reported as means and standard deviations. A mean describes the average observed change in an arm. A standard deviation describes how spread out individual changes are around that average. These summaries answer different questions: the mean locates the centre of the observed changes, while the standard deviation describes variation among participants.

What does the mean difference represent?

The primary contrast is the mean change in the IGlar OD arm minus the mean change in the IDeg 3TW arm. The reported estimate is -0.4. The sign depends on this subtraction order. A negative estimate means the IGlar OD group had a more negative mean change than the IDeg 3TW group. It is a comparison of group averages, not a statement that each participant's outcome moved by that amount.

For continuous outcomes, a mean difference retains the outcome's original units. The HbA1c endpoint is expressed as a percentage of glycosylated haemoglobin, while body weight is expressed in kg. A standardized effect can also describe the contrast relative to pooled variability, but it is less directly interpretable in the original clinical units. The registry's posted comparison includes a standardized effect estimate, but interpretation of the main clinical contrast is clearest in the original endpoint scale.

Why use a confidence interval?

A confidence interval gives a range of values compatible with the observed data under the analysis assumptions and method used. It conveys precision as well as direction: a narrower interval indicates greater precision than a wider interval, while an interval spanning zero is compatible with no mean difference under that framework. The posted interval for the primary mean difference lies entirely below zero; the interval for body-weight change spans zero. The registry record does not state the confidence level, so no confidence percentage should be attached to these intervals based on the record alone.

A confidence interval is not a range containing a fixed percentage of individual participant outcomes. Nor does an interval by itself establish clinical importance. It describes uncertainty in the estimated group contrast, not the spread of responses in either arm. The standard deviations address within-arm spread; the confidence interval addresses uncertainty about the estimated difference.

What does the p-value tell us?

The unadjusted p-value for the primary comparison is <0.001, and the unadjusted p-value for body-weight change is 0.559. A p-value describes how unusual results at least as inconsistent with a null comparison would be under the assumptions of the statistical test, if the null hypothesis were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. “Unadjusted” means that the reported value is not described as adjusted for multiple outcome or comparison testing.

The record does not report the exact statistical model or test used for the primary analysis. Consequently, the results can be interpreted as the posted unadjusted summary comparison, but additional details such as covariate adjustment, model diagnostics, or handling of distributional features beyond the stated LOCF procedure are not available in the registry record.

Why does variability matter?

Participants can have different changes even when assigned to the same arm. Standard deviations of 0.95 and 1.07 for the primary outcome summarize that variability. Standard errors, by contrast, describe precision of an estimated mean and depend on both variability and the number of observations. They are not interchangeable with standard deviations. The posted summaries include standard deviations, and the comparison calculations also use standard errors, but the standard errors are not necessary for reading the central clinical contrast.

Many common comparisons of means rely on assumptions about the sampling distribution or the form of the outcome data. General statistical practice checks whether such assumptions are reasonable, and may use robust or alternative approaches if they are not. The registry record does not report diagnostic checks or alternative analyses, so no conclusion about those procedures can be drawn. The reported mean and standard deviation are useful summaries, but they do not show the complete shape of the outcome distribution.

What is the role of randomisation?

Random allocation is intended to make the treatment groups comparable on average at the start of a trial, including for factors that may not be measured. It supports causal interpretation of between-arm comparisons when allocation, follow-up, and analysis are implemented appropriately. The registry records randomisation and a parallel-group model, but does not describe the sequence generation or allocation concealment. Randomisation does not remove uncertainty, guarantee exact balance in every characteristic, or prevent bias arising after assignment.

Because the trial is recorded as having no masking, participants and investigators may have known the assigned treatment. That design fact can matter for outcomes influenced by reporting, behaviour, or assessment. The primary outcome is a laboratory measure, but the registry summary does not provide enough information to assess how knowledge of assignment affected conduct or assessment. The record also does not state whether outcome assessors were masked.

How should missing data be understood?

The Full analysis set included all randomised subjects, and missing values were imputed using last observation carried forward. LOCF substitutes a participant's last observed value for a later missing value in the analysis. It therefore avoids dropping a participant solely because a later value is absent, but it can understate or overstate later change if the outcome would have continued to move after the last observation. Its suitability depends on why data are missing and how outcomes evolve. The registry record does not report missingness counts, reasons, or sensitivity analyses, so the consequences of this assumption cannot be quantified.

These methods concepts help distinguish what the posted numbers say from what remains unknown. The registry supplies group summaries, an unadjusted mean difference, interval estimates, p-values, and an analysis-population and imputation description. It does not report a full statistical analysis plan, model specification, diagnostic work, or sensitivity analyses. Interpretation should therefore remain anchored to the stated summaries rather than assuming unreported procedures.

11. Confidence Intervals and Precision

The primary mean difference is -0.4, and the posted interval has both bounds below zero. This indicates that the range of values compatible with the reported analysis is on the negative side of zero, rather than including no difference. The interval gives more information than the point estimate alone: it communicates uncertainty around the estimated contrast. The p-value is <0.001, consistent with the interval's exclusion of zero under the reported unadjusted analysis.

Precision is not the same as clinical importance. An estimate can be statistically precise without being large enough to matter clinically, and an uncertain estimate can still include values that would matter. The registry record does not report a threshold for a clinically important HbA1c difference, so the interval cannot be judged against such a threshold. It also does not report the confidence level used to construct the intervals; the interval's bounds can be described, but a confidence percentage is not stated.

The body-weight mean difference is 0.2 kg, and its interval includes zero; the unadjusted p-value is 0.559. That interval is consistent with a range of possible contrasts on either side of no difference, so the estimate is less decisive about direction. This is not evidence that the arms are equivalent. Demonstrating equivalence or non-inferiority requires a prespecified margin and an analysis designed for that purpose, neither of which is reported in the registry record.

For both outcomes, the standard deviations describe observed participant-level spread, whereas the interval describes uncertainty in the mean difference. The registry record does not provide individual observations, so readers cannot independently assess distribution shape or the influence of extreme values. Precision is therefore best interpreted as precision of the posted group-level comparison under its analysis assumptions, not as certainty about each participant's outcome.

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 a report of the trial's original design calculation. For these continuous outcomes, the displayed counts are participants per arm, not total events. The stated 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 set to the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a planning scenario with an 80% chance of detecting the specified effect if that effect were true, under the listed assumptions. The 90% power column describes the corresponding planning target with a 90% chance. These are design illustrations, not guarantees about the outcome of a future study. They depend on the assumptions used, including the effect size and the statistical approach.

Each row represents planning for a different fraction of the observed effect: 100%, 75%, or 50%. Smaller effects need more participants to be detected with the same target power, which is why the planning counts increase as the assumed effect becomes smaller. For body-weight change, the observed mean difference is small relative to the variability, and the resulting planning counts are much larger than those for the primary endpoint. This illustrates how both the target effect and outcome variability influence planning.

These sample-size figures are not observed power. Observed power calculated from the estimated effect would add little beyond the observed estimate and its uncertainty; the useful role of the figures is to illustrate how design requirements change under stated planning scenarios. The figures should not be read as evidence that the completed trial was planned around those assumptions, because the original design justification is not reported.

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 = -0.400; pooled standard deviation σ = 1.012.
2. n = 2 × (1.96 + 0.842)² × 1.012² / -0.400² = 100.5, rounded up to 101 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 <- -0.4                      # observed difference in means
sigma <- 1.01191166011538                     # 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(1068678)
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 = 101 (80% power), 135 (90% power)
 75% of observed effect: n per arm = 179 (80% power), 240 (90% power)
 50% of observed effect: n per arm = 402 (80% power), 538 (90% power)
power.t.test: 101.4 
Simulated power at n = 101 per arm: 0.799 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, comparison, subgroup, or analysis. As the number of statistical tests grows, so does the chance that at least one test will appear unusual under a null scenario, even if no true difference exists. Researchers can address this issue through prespecified outcome hierarchies, adjusted significance thresholds, or other planned procedures. The registry record does not report a multiplicity adjustment or a testing hierarchy. The posted p-values are unadjusted, so they should be read as individual comparisons rather than as family-wise controlled evidence.

The registry lists two outcome measures: the primary change in HbA1c and the secondary change in body weight. It does not report the complete set of outcomes assessed during the trial or whether other analyses were performed. The secondary analyses field contains no reported analyses. Absence of these details does not prove that no other analyses occurred; it means the registry record does not provide them. This limits assessment of selective reporting and of how the reported results relate to the study's full analysis plan.

For the primary endpoint, the Full analysis set included all randomised subjects, with missing data imputed by last observation carried forward. The registry notes that one subject was randomised despite being a screening failure. The record does not report the number or pattern of missing primary outcome measurements, reasons for missingness, or sensitivity analyses using alternative assumptions. LOCF produces an analyzable value by carrying forward a prior observation, but the estimate can be sensitive to whether that carried-forward value is a reasonable representation of the missing later measurement.

The body-weight summaries use arm counts of 227 and 229, while the primary endpoint summaries use 229 and 230. The registry record does not explain the difference in analyzed counts or report details of missingness for body weight. Without participant-level information or further analysis documentation, it is not possible to determine whether missingness could have affected the secondary comparison.

The record also does not report interim analyses, stopping rules, subgroup plans, a detailed statistical analysis plan, or the original sample-size justification. Those items should not be inferred from the posted estimates or from the fact that the trial is marked completed. Together, these reporting gaps mean that the primary result can be interpreted as reported, but its sensitivity to alternative analytical choices and the broader multiplicity context cannot be fully evaluated.

15. 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: angina unstable (0.9%), non-cardiac chest pain (0.4%), appendicitis (0.4%), cellulitis (0.4%), ankle fracture (0.4%).

The registry reports serious adverse events for 11 of 227 participants at risk in the IDeg 3TW group and 4 of 229 at risk in the IGlar OD group. It also reports other adverse events for 69 of 227 and 77 of 229, respectively. These are counts of affected participants and the corresponding numbers at risk, not a complete description of the nature, timing, duration, or severity of every event.

The serious-event terms listed include angina unstable at 0.9%, non-cardiac chest pain at 0.4%, appendicitis at 0.4%, cellulitis at 0.4%, ankle fracture at 0.4%, and forearm fracture at 0.4%. The registry entry does not identify the arm attribution for these listed terms in the available summary, so they should not be assigned to a treatment group. Deaths are not reported in the registry record.

Counts alone do not establish that one treatment caused more or fewer events. Interpreting safety comparisons also requires context such as exposure, event definitions, follow-up, and handling of repeated events. The available record supplies the listed counts but does not report enough detail to make those additional assessments. These figures describe posted safety reporting and are not a complete safety profile.

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

The primary result describes a difference in average HbA1c change between two randomised groups at Week 26. The posted estimate is -0.4 for IGlar OD relative to IDeg 3TW, with an interval wholly below zero and an unadjusted p-value of <0.001. Statistically, this is evidence of a difference between the reported group means under the analysis used. It is not a direct statement about the outcome of every participant or about the size of benefit for any particular person.

Statistical evidence and clinical relevance are distinct. A small p-value does not establish that a difference is important to patients, and a mean difference does not describe all individual experiences. The registry record does not provide a threshold for a clinically meaningful HbA1c change, detailed individual outcomes, or additional evidence needed to place the contrast in a broader clinical context. The result should therefore be described in terms of the posted measurement and analysis, without turning it into treatment advice.

The secondary body-weight comparison has an interval including zero and an unadjusted p-value of 0.559. This is an uncertain estimate, not proof that the treatments have the same effect on weight. The safety counts likewise describe recorded adverse events but do not establish causation or a comparative safety conclusion. The available registry summary does not give full details on event timing, exposure, or all safety analyses.

The trial's randomized parallel design supports a between-group comparison, but interpretation is also shaped by the recorded absence of masking, the LOCF imputation for missing primary data, and the lack of reported sensitivity analyses. The registry does not report the original sample-size justification, full statistical analysis plan, or multiplicity procedures. These limitations do not erase the posted result; they define the boundaries of what can be concluded from the record.

In short, the posted data show a statistically distinguishable mean HbA1c change at Week 26 and a less conclusive secondary body-weight comparison. They do not, on their own, establish clinical importance, explain the mechanism of any difference, predict an individual's response, or provide a complete assessment of benefits and risks. Those questions require evidence beyond the aggregate registry summaries.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares average changes in a continuous primary outcome across randomised parallel groups and reports both within-arm variability and a between-arm estimate. Looking at the mean difference alongside the arm means prevents the comparison from being reduced to whether each group changed from baseline. The contrast, rather than a within-group change considered alone, is the relevant randomized comparison.

The result also illustrates why precision and significance should be read together. The primary estimate is accompanied by an interval that excludes zero and an unadjusted p-value of <0.001. The secondary estimate has an interval that includes zero and an unadjusted p-value of 0.559. These patterns show how the interval and p-value can communicate uncertainty differently across outcomes, while neither measure answers whether a difference is clinically important.

The record makes several analysis features visible: the Full analysis set included all randomised subjects, missing primary data were handled with LOCF, and the primary outcome was measured at Week 26. These details matter because population definitions, timing, and missing-data assumptions shape the result being estimated. The different arm counts for primary and secondary summaries also highlight why the analyzed population should be checked for each endpoint.

The planning illustrations provide a further statistical lesson. Required sample size depends on the effect targeted and the variability of the outcome, so planning for smaller effects requires more participants. Those illustrations are not the original design calculation and must not be mistaken for observed power. The registry does not report the original sample-size justification, which limits assessment of the study's planning rationale.

Finally, the record demonstrates the value and limits of registry reporting. It provides the central endpoint estimates, some safety counts, and key population details, while leaving the full multiplicity plan, analysis model, missing-data sensitivity work, and several implementation details unreported. Statistical interpretation is strongest when these reported estimates are read with their assumptions and boundaries in view.

18. Limitations

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

Several limitations are specific to the registry summary. The primary outcome uses LOCF for missing data, but the record does not report how many measurements were missing, why they were missing, or whether alternative missing-data analyses were conducted. The impact of carrying forward earlier observations therefore cannot be evaluated. The registry also notes one randomised subject was a screening failure but does not explain how this fact affected the analysis.

The entry records no masking. It does not describe allocation concealment, who knew treatment assignments, whether outcome assessors were masked, or the detailed procedures used to collect outcomes. Those omissions leave uncertainty about possible influences on trial conduct or outcome assessment. The primary endpoint is a laboratory measure, but this alone does not resolve questions about study implementation.

The registry provides one secondary outcome and its summary comparison, but does not report a complete multiplicity strategy or the full statistical analysis plan. It also does not report an adjusted primary model, diagnostic checks, sensitivity analyses, subgroup analyses, or interim analyses. The unadjusted results cannot be assumed to have undergone procedures that are not stated in the record.

For safety, counts at risk and affected participants are available, along with selected serious-event terms. The record does not provide full event-level detail, treatment attribution for the listed terms, timing, exposure-adjusted summaries, or deaths. As a result, the posted figures cannot serve as a complete comparison of safety profiles.

The registry states that enrollment was 460, while the posted outcome summaries have their own arm counts; the record does not explain all differences in analyzed counts between outcomes. It also does not report the original sample-size assumptions or justification. These limitations do not change the arithmetic of the posted summaries, but they constrain assessment of reporting completeness, robustness, and the intended precision of the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of NN1250 With Insulin Glargine in Subjects With Type 2 Diabetes — NCT01068678.
• Registry record last updated 2017-03-06; status last verified 2017-01.
• Results first posted 2015-12-28.
• 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.

22. Record Summary

The registry describes NCT01068678, a completed Phase 3 randomized parallel-group trial sponsored by Novo Nordisk A/S. It compared insulin degludec (IDeg 3 times weekly) with insulin glargine (IGlar OD) in subjects with type 2 diabetes receiving metformin alone or with an oral anti-diabetic drug and qualifying for intensified treatment. The record lists enrollment of 460, a start of 2010-02, and primary completion of 2010-11.

The primary endpoint was change from baseline in HbA1c at Week 26. The Full analysis set included all randomised subjects, with missing data imputed using LOCF; the record notes one randomised subject was a screening failure. The posted mean difference was -0.4 for IGlar OD relative to IDeg 3TW, with an unadjusted p-value of <0.001. Change in body weight was the listed secondary outcome, with an unadjusted p-value of 0.559. The record also reports serious and other adverse-event counts, but does not report deaths.

The summary does not report the original sample-size justification, full analysis plan, multiplicity procedures, or sensitivity analyses for missing data. Its estimates should be read as posted results under the stated population and imputation approach.