Comparison of Subject-driven Titration of Biphasic Insulin Aspart (BIAsp) 30 Twice Daily Versus Investigator-driven Titration of BIAsp 30 Twice Daily Both in Combination With Oral Antidiabetic Drugs in Subjects With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Subject-driven Titration of Biphasic Insulin Aspart (BIAsp) 30 Twice Daily Versus Investigator-driven Titration of BIAsp 30 Twice Daily Both in Combination With Oral Antidiabetic Drugs in Subjects With Type 2 Diabetes (NCT01618214), a randomized phase 4 study. The primary outcome is Change From Baseline in HbA1c (Glycosylated Haemoglobin).

2. Clinical Question

3. Trial Design

This was a phase 4, randomized, open-label, two-arm parallel-group trial. The title describes a 20-week comparison of subject-driven versus investigator-driven titration of biphasic insulin aspart 30, both twice daily and combined with oral antidiabetic drugs. The registry lists enrollment as 344 and trial status as completed. It records a start in 2012-06 and primary completion in 2013-01.

The trial focused on people with type 2 diabetes inadequately controlled with premixed human insulin. It was conducted in Asia, and the background oral therapy was described as metformin, with or without an alpha-glucosidase inhibitor. The registry lists biphasic insulin aspart 30 as the drug intervention. The arm descriptions themselves are empty, so further operational details about titration schedules, dose targets, or treatment procedures are not reported in the registry record.

Random assignment is intended to make the treatment groups comparable on average at the start of a trial, although it cannot ensure that every measured or unmeasured feature is balanced. The parallel-group design means that each participant was assigned to one of the titration approaches rather than crossing between them. Because the trial was open-label, participants and investigators knew which approach was being used; whether any outcome assessors were masked is not reported in the registry record.

The main outcome was change from baseline in HbA1c, measured at week 0 and week 20. The primary analysis is described as an estimate of mean change at 20 weeks in the full analysis set, with last observation carried forward used for missing data when a post-randomisation measurement existed. The registry’s primary outcome summary lists 168 subjects in the subject-driven group and 170 in the investigator-driven group. The registry’s enrollment figure and analysis-set counts serve different purposes and should not be treated as interchangeable descriptions of the analysis population.

The original trial’s sample-size justification, planned allocation details, protocol-defined analysis plan, and interim analysis arrangements are not reported in the registry record. The sample-size display associated with the posted results is a planning illustration based on observed effects, not a record of the trial’s original design calculations.

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: Eligible subjects were randomised in a 1:1 manner to one of the 2 treatment groups.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) - included all randomised subjects and missing data was imputed using last observation carried forward (LOCF) where any post-randomisation measurements were available. Six subjects did not contribute to FAS due to lack of post-randomisation measurements.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in HbA1c (Glycosylated Haemoglobin), measured over Week 0, week 20.

HbA1c, or glycosylated haemoglobin, is a continuous measure used to describe average blood-glucose exposure over a period of time. The primary outcome was its change from baseline, expressed as a percentage of glycosylated haemoglobin, between week 0 and week 20. A change score compares each group’s follow-up measurement with its baseline level; a negative mean change indicates that the group’s mean follow-up value was lower than its mean baseline value.

Using a continuous endpoint retains information about the size and direction of changes across participants. It can therefore be more informative than reducing the outcome to whether each participant crossed a particular threshold. The registry also lists threshold-based HbA1c outcomes among secondary measures, but their numerical results are not reported in the registry record.

HbA1c is relevant to a comparison of glucose-management approaches because it describes glycaemic status using a laboratory measure rather than relying only on a treatment-process measure such as how a dose is adjusted. A change-from-baseline outcome also takes the starting value into account in the reported group summaries. However, the registry’s sponsor analysis is labelled as a comparison of final values, so its estimand is not identical in wording to the primary change outcome.

The posted primary outcome is an estimated mean change in the full analysis set. The record describes last observation carried forward for missing data when post-randomisation measurements were available and notes that six subjects lacked such measurements. The implications of this missing-data approach depend on assumptions about how missing outcomes relate to observed outcomes; those assumptions are not reported in the registry record.

7. Results Posted in the Registry

• Investigator-driven Titration: mean -1.31 versus -1.32 on control; difference 0.01 (95% CI -0.18 to 0.20), standardized effect d = 0.01; z-test p = 0.920.

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 FPG (Fasting Plasma Glucose)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Investigator-driven Titration: mean -1.48 versus -1.26 on control; difference -0.22 (95% CI -0.82 to 0.38), standardized effect d = -0.08; z-test p = 0.472.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Investigator-driven Titration and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies secondary outcomes covering HbA1c thresholds, fasting plasma glucose change, and hypoglycaemic episodes. Numerical results are posted for fasting plasma glucose change; results for achieving HbA1c below 7.0%, achieving HbA1c below or equal to 6.5%, and the listed hypoglycaemia categories are not reported in the registry record. The available secondary-outcome evidence is therefore incomplete.

The fasting plasma glucose summaries show mean changes of -1.26 mmol/L in the subject-driven group and -1.48 mmol/L in the investigator-driven group. The recalculated unadjusted mean difference is -0.22 mmol/L, with a 95% confidence interval from -0.819 to 0.379 and an unadjusted p-value of 0.472. The interval includes zero and is broad relative to the point estimate. No sponsor-reported analysis is listed for this secondary outcome.

In broad terms, the posted secondary information does not provide a clear, precise contrast that overturns the primary comparison’s pattern of close group summaries. That statement is limited by the sparse registry reporting: the unreported threshold and hypoglycaemia results cannot be used to confirm or contradict the available outcomes. The secondary record should not be treated as a complete overview of all outcomes named in the trial record.

Secondary outcomes often address additional dimensions of efficacy or safety, but interpreting several outcomes increases the chance that at least one result may appear notable by chance. General statistical explanation: multiplicity is the problem created by making multiple comparisons or testing multiple outcomes; without appropriate adjustment or a prespecified hierarchy, nominal p-values can overstate the strength of evidence. The registry does not report a multiplicity adjustment or a hierarchy for secondary outcomes. Accordingly, unadjusted secondary findings carry less weight than the primary outcome and should be interpreted as supportive or exploratory rather than as independent confirmation.

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

• Percentage of Subjects Achieving HbA1c Below 7.0%
• Percentage of Subjects Achieving HbA1c Below or Equal to 6.5%
• Change From Baseline in FPG (Fasting Plasma Glucose)
• Incidence of Hypoglycaemic Episodes (All, Major, Minor and Symptoms Only)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: HbA1c change from baseline. For a continuous outcome, a group mean describes the average observed change, while the standard deviation describes how spread out individual measurements are around that mean. The posted mean changes were -1.32 for subject-driven titration and -1.31 for investigator-driven titration; the respective standard deviations were 0.86 and 0.96. These measures answer different questions: the means describe average change, and the standard deviations describe variation among observations.

What does a mean difference represent?

The unadjusted comparison expresses the investigator-driven group’s mean relative to the subject-driven group’s mean. Its estimated difference is 0.01 percentage points. A value near zero indicates that the two posted means are close on this scale, but the estimate is subject to sampling uncertainty. The recalculated comparison uses the posted group summary statistics and is not a replacement for a model-based analysis using participant-level data.

General statistical explanation: a standard error describes the expected sampling variability of an estimate under the assumptions of its calculation. It is different from a standard deviation, which describes variability among individual observations. The registry-based recalculation lists standard errors of 0.066 and 0.074 for the two primary arm means. The uncertainty in a difference depends on the uncertainty in both group means and on the calculation’s assumptions.

How should the confidence interval be read?

General statistical explanation: a confidence interval is a range produced by a method that, over repeated use under its assumptions, would capture the underlying parameter at the stated rate. It is not a range containing a specified proportion of individual participant outcomes, and it is not a probability statement about the fixed true effect after the interval has been calculated. The recalculated interval for the mean difference runs from -0.184 to 0.204 at the 95% level. Its inclusion of zero means the unadjusted interval is compatible with no difference, as well as with small differences in either direction.

The posted recalculation uses a pooled standard deviation of 0.912 and reports a standardized difference of 0.011. These are summary-scale quantities intended to express the observed contrast relative to variability. They do not determine whether a difference matters clinically. The registry does not report a threshold for a clinically important difference, so a clinical-importance judgment cannot be inferred from these values alone.

Why does the sponsor analysis differ in form?

The sponsor-reported analysis is labelled regression, linear, and its parameter is mean difference in final values. It gives -0.02, with a 95% confidence interval from -0.19 to 0.14, and is categorized as non-inferiority or equivalence. The recalculation instead compares the posted change-from-baseline means using an unadjusted approach. Final-value and change-score analyses can answer related but distinct questions. The registry does not report the model specification or the non-inferiority margin, so the exact adjustments and decision criterion cannot be reconstructed from the record.

General statistical explanation: regression can account for selected covariates or baseline measurements when those terms are included in the model. This can produce an estimate and interval that differ from a simple comparison of group summaries. The word “regression” alone does not reveal which covariates were included, how model assumptions were assessed, or whether any additional adjustments were made. Those details are not reported in the registry record.

What does over-dispersion mean for count outcomes?

General statistical explanation: over-dispersion occurs when observed variation in count data exceeds what a simple count model expects. When that happens, a model that assumes less variability than the data contain can understate uncertainty. This is relevant in principle to outcomes such as hypoglycaemic episodes, which may be counted, but the registry does not post numerical results or an analysis method for those outcomes. It is therefore not possible to determine whether over-dispersion was present or how it was handled in this trial.

For the continuous fasting plasma glucose outcome, the registry reports mean changes and standard deviations, and the recalculation uses those summaries to form an unadjusted comparison. No sponsor-reported analysis is listed for that secondary outcome. The same general distinction applies: a summary-based recalculation describes the posted group-level information, while the trial’s original analysis could involve methods that are not documented in the registry record.

These methods should not be conflated with power. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under the model assumptions; it is not the probability that the null hypothesis is true. A confidence interval communicates uncertainty in an estimate, while sample-size calculations describe planning scenarios under stated assumptions. The posted planning illustration is not an estimate of the trial’s observed power.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 0.01 percentage points, with a 95% confidence interval from -0.184 to 0.204. The interval spans zero, so the simple unadjusted result does not establish a directional difference. Its width also shows that the calculation does not pin the difference down to a single value. It remains compatible with modest differences favoring either group on the reported scale.

The sponsor’s regression result has a 95% confidence interval from -0.19 to 0.14 around a mean difference of -0.02. This is a separate estimate based on the sponsor’s reported analysis of final values. The two intervals are similar in broad terms, but they should not be treated as identical: the estimands and analytical approaches are described differently in the registry record. For formal interpretation of the sponsor analysis as a non-inferiority or equivalence analysis, the margin and decision rules are needed; these are not reported in the registry record.

General statistical explanation: narrower intervals indicate greater precision for an estimate under the chosen method, while wider intervals indicate more uncertainty. Precision is not the same as clinical importance. An interval can be narrow around a small effect, or broad enough to include effects that might be considered important; interpreting that requires a clinically justified threshold, which is not reported in the registry record.

The unadjusted p-value of 0.92 does not show that the groups are equivalent. It indicates that the observed unadjusted difference is not unusual under a no-difference model, given the calculation’s assumptions. A failure to identify a difference is not proof that the true difference is zero. Likewise, the sponsor’s category label does not by itself resolve the question of equivalence without the margin and full analysis details.

Precision is also affected by the analysis population and missing-data handling. The primary outcome description specifies the full analysis set and last observation carried forward for subjects with post-randomisation measurements. The registry notes six subjects without such measurements. The record does not provide sensitivity analyses or enough detail to assess how alternative missing-data assumptions would affect the interval.

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 display gives planning illustrations for the continuous primary outcome. Its entries are participants per arm, not total participants across both arms. It is based on the observed effect, with scenarios planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the planning calculation indicates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design concepts: power refers to the probability of detecting an effect of the specified size if that effect is present and the calculation assumptions hold. The figures are not results from the completed trial.

For the primary outcome, the display lists 130,471 participants per arm for planning around 100% of the observed effect at 80% power, and 174,664 participants per arm at 90% power. For the 75% effect scenario, it lists 231,948 and 310,513 participants per arm. For the 50% effect scenario, it lists 521,883 and 698,653 participants per arm. Smaller effects require more participants to detect under the same assumptions, which explains why the planning figures rise as the target effect fraction gets smaller.

These are planning illustrations computed from the observed effect, not observed power and not the trial’s original design justification. The trial’s own original sample-size assumptions are not reported in the registry record. The planning figures should therefore not be read as a claim that the trial was designed to detect a particular effect or as a retrospective assessment of whether it had adequate power.

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 = 0.010; pooled standard deviation σ = 0.912.
2. n = 2 × (1.96 + 0.842)² × 0.912² / 0.010² = 130,470.6, rounded up to 130,471 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 <- 0.01                      # observed difference in means
sigma <- 0.911669713584183                     # 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(1618214)
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 = 130,471 (80% power), 174,664 (90% power)
 75% of observed effect: n per arm = 231,948 (80% power), 310,513 (90% power)
 50% of observed effect: n per arm = 521,883 (80% power), 698,653 (90% power)
power.t.test: 130471.6 
Simulated power at n = 130,471 per arm: 0.800 (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 a sponsor analysis using linear regression, with the parameter described as mean difference in final values. The reported estimate is -0.02, with a 95% confidence interval from -0.19 to 0.14. The record classifies this analysis as non-inferiority or equivalence. No p-value is reported for that analysis, and the non-inferiority or equivalence margin is not reported in the registry record.

The recalculated comparison is an unadjusted analysis of the posted primary change-from-baseline means and standard deviations. It estimates a difference of 0.01, with a 95% confidence interval from -0.184 to 0.204 and an unadjusted p-value of 0.92. Since the record does not flag a discrepancy, the recalculation is broadly consistent with the close group summaries, but it does not supersede the sponsor’s own analysis.

The estimates are not directly interchangeable. The sponsor result is described as a regression comparison of final values, whereas the recalculation uses change-from-baseline summaries and does not adjust for covariates. Differences in endpoint formulation and analysis method can lead to different estimates and intervals. The registry does not give enough model detail to reproduce the sponsor result.

The sponsor’s analysis takes precedence as the trial’s own reported analysis. However, its classification as non-inferiority or equivalence does not allow the reader to verify that conclusion without the prespecified margin and full analysis details. The posted information supports reporting the sponsor estimate and interval, but not reconstructing the decision rule behind the category.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes in addition to the primary HbA1c change outcome. It does not report whether the trial used a multiplicity adjustment, a testing hierarchy, or another method to control the chance of false-positive findings across outcomes. Without that information, unadjusted results from multiple endpoints should not be interpreted as if each were the sole prespecified test. Numerical results for several listed secondary outcomes are not reported in the registry record.

The primary analysis population is described as the full analysis set, including randomized subjects when post-randomisation measurements were available. Missing data were imputed using last observation carried forward where any post-randomisation measurements were available. Six subjects did not contribute to the full analysis set because they lacked post-randomisation measurements. The registry does not state how missing measurements were handled for every secondary outcome, whether other imputation methods were considered, or whether sensitivity analyses were conducted.

General statistical explanation: last observation carried forward fills a missing later value using the participant’s last observed value. This can be simple to implement, but it assumes that carrying the earlier value forward is a reasonable representation of what would otherwise have been observed. If outcomes change after the last measurement, or if missingness is related to the unobserved outcome, the resulting estimate can be biased. The direction and size of any such effect cannot be determined from the registry record.

The record does not report whether the analysis followed an intention-to-treat principle in the strict sense, how protocol deviations were handled, or whether additional analysis populations were used for the sponsor’s non-inferiority or equivalence analysis. The phrase “full analysis set” and the brief description of missing-data handling do not supply those details. The original sample-size justification, interim analyses, and complete statistical analysis plan are also not reported in the registry record.

These reporting gaps matter because the interpretation of a close estimate depends not only on the numerical result but also on prespecified methods, missing-data assumptions, and the handling of multiple outcomes. They do not change the posted summaries, but they limit independent assessment of the robustness of the conclusions.

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: coronary artery disease (0.6%), meniere (0.6%), gastritis (0.6%), brain contusion (0.6%), heat stroke (0.6%).

The serious adverse event counts are recorded for groups with 172 subjects at risk in each group. The registry lists 4 subjects affected by serious adverse events in the subject-driven group and 7 in the investigator-driven group. It also lists other adverse events affecting 1 subject in the subject-driven group and 13 in the investigator-driven group. These are counts from the safety record, not a complete comparison of event rates or a causal assessment.

The most frequently listed serious-event terms are coronary artery disease, Meniere, gastritis, brain contusion, heat stroke, and patella fracture, each reported as 0.6%. The registry does not provide further detail about event timing, severity beyond the serious classification, relatedness to treatment, or how terms were coded. Death counts are not reported in the registry record.

General statistical explanation: adverse-event counts should be interpreted with attention to how events were defined, how long participants were observed, and whether participants could experience more than one event. The posted subject counts do not establish that titration approach caused an event or that one approach is safer. The record does not provide the detail needed for a broader safety comparison, and these figures should be read as descriptive reporting.

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

The posted primary summaries show similar mean HbA1c changes in the two titration groups over the 20-week treatment period: -1.32 in the subject-driven group and -1.31 in the investigator-driven group. The recalculated difference is small, and its confidence interval includes zero. The sponsor’s own analysis also reports a mean difference close to zero with an interval that includes zero.

These results do not prove that the two approaches are identical. A failure to detect a difference is not the same as demonstrating equivalence. Equivalence and non-inferiority require a prespecified margin that defines how large a difference can be while still meeting the intended criterion. Although the registry labels the sponsor analysis as non-inferiority or equivalence, the margin and decision rules are not reported in the registry record, so that conclusion cannot be independently evaluated from the posted information alone.

The reported means describe group averages, not the experience of every participant. Standard deviations indicate that individual outcomes varied around those averages. The estimates also apply to the analysis population and endpoint definition recorded for this trial, including its stated missing-data approach; they should not be assumed to apply unchanged to other populations, settings, follow-up periods, or treatment procedures.

The registry also identifies secondary outcomes and safety events, but the numerical information is incomplete. In particular, results for several named secondary outcomes are not reported in the registry record. This limits the ability to form a comprehensive view across outcomes. The safety counts are descriptive and do not establish whether events were caused by treatment.

Statistically, the clearest interpretation is that the posted primary group summaries are close and that the uncertainty interval remains compatible with small differences in either direction. The record does not justify a claim that one strategy is superior, that the approaches are interchangeable, or that there is no meaningful difference. Those claims would require clinical thresholds and design details not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates an important distinction between comparing observed averages and proving equivalence. The arm-level HbA1c changes are close, and the recalculated difference is near zero, but a near-zero point estimate alone cannot establish that two treatment approaches are equivalent. A formal equivalence or non-inferiority interpretation depends on a prespecified margin and an analysis that evaluates the interval against that margin.

It also highlights how the analytical question affects the reported estimate. The sponsor analysis is described as a regression comparison of final values, while the simple recalculation compares change-from-baseline summaries. Both can be informative, but they answer differently specified questions and rely on different methods. Keeping those distinctions clear prevents a reader from treating a recalculation as a reproduction of the trial’s own analysis.

The registry’s missing-data description is another statistically important feature. The primary outcome uses last observation carried forward for subjects with post-randomisation measurements, while subjects without any such measurement did not contribute to the full analysis set. This makes the analysis population and imputation approach relevant to interpreting the estimate, not merely administrative details.

Finally, the record demonstrates the limits of a partial results record. Multiple secondary outcomes are named, but numerical results are absent for several of them, and details about multiplicity, the original sample-size justification, and the sponsor model are not reported. Statistical interpretation depends on understanding both the estimates and the design decisions that produced them. Where those details are missing, conclusions should remain proportionate to the reported evidence.

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 registry record gives limited detail about how titration was implemented. The arm descriptions are empty, and dose-adjustment procedures, targets, adherence, and treatment exposure details are not reported in the registry record. These omissions constrain assessment of what distinguished the two approaches in practice beyond who drove titration.

The trial was open-label. Knowledge of treatment assignment can affect participant and investigator behaviour, and the registry does not report whether outcome assessors were masked. HbA1c is a laboratory measure, but the record does not supply enough information to assess all possible pathways through which open-label conduct might influence treatment or follow-up.

The primary outcome uses last observation carried forward when post-randomisation measurements were available. The registry notes six subjects without post-randomisation measurements who were excluded from the full analysis set, but does not report sensitivity analyses using alternative assumptions. The adequacy of the imputation cannot be established from the posted description.

The sponsor analysis is categorized as non-inferiority or equivalence, but the margin, model covariates, and detailed decision criteria are not reported in the registry record. The recalculation is unadjusted and uses summary statistics, so it cannot reproduce participant-level modeling or resolve the formal non-inferiority question. The original sample-size justification and planned statistical analysis are also not reported.

Reporting of secondary outcomes is incomplete. The registry lists HbA1c threshold outcomes and hypoglycaemia measures, but their numerical results are not reported. Multiplicity handling is not described. Safety information gives selected counts and serious-event terms without fuller event-level context, and deaths are not reported in the registry record.

The registry records the trial as conducted in Asia and describes a 20-week treatment comparison in people inadequately controlled with premixed human insulin. The record does not establish how well the findings generalize beyond that setting, treatment duration, or study population. These limitations do not invalidate the posted estimates, but they restrict how far they can be interpreted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparison of Subject-driven Titration of Biphasic Insulin Aspart (BIAsp) 30 Twice Daily Versus Investigator-driven Titration of BIAsp 30 Twice Daily Both in Combination With Oral Antidiabetic Drugs in Subjects With Type 2 Diabetes — NCT01618214.
• Registry record last updated 2017-02-24; status last verified 2017-01.
• Results first posted 2014-05-08.
• 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

NCT01618214 is a completed phase 4, randomized, open-label, two-arm parallel-group trial comparing subject-driven with investigator-driven titration of biphasic insulin aspart 30 twice daily, both with oral antidiabetic drugs. The trial enrolled 344 and focused on people with type 2 diabetes inadequately controlled with premixed human insulin. Its primary outcome was mean change from baseline in HbA1c at week 20.

The posted arm means were -1.32 for subject-driven titration and -1.31 for investigator-driven titration. The sponsor’s regression analysis of final values reported a mean difference of -0.02 with a 95% confidence interval from -0.19 to 0.14; the registry categorizes it as non-inferiority or equivalence but does not report the margin. The unadjusted recalculation is close to zero, with a 95% confidence interval from -0.184 to 0.204.

Interpretation is limited by missing details about the statistical plan, non-inferiority margin, multiplicity, and several secondary outcomes. The primary outcome used last observation carried forward where post-randomisation measurements were available.