A Comparison of Two Treatment Strategies in Older Participants With Type 2 Diabetes Mellitus (T2DM): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Comparison of Two Treatment Strategies in Older Participants With Type 2 Diabetes Mellitus (T2DM) (NCT02072096), a randomized phase 4 study. The primary outcome is Percentage of Participants Achieving and Maintaining Individualized Glycated Hemoglobin A1c (HbA1c) Targets Without Clinically Significant Hypoglycemia.

2. Clinical Question

3. Trial Design

The registry record describes IMPERIUM as a Phase 4, randomized, controlled, parallel-group study. It compared two treatment strategies for participants aged 65 and older with type 2 diabetes mellitus. The study was open-label, meaning that masking was not used. The record lists Eli Lilly and Company as sponsor and gives 192 as the enrollment figure.

The strategies differed in their organizing principle, not simply in a single drug. Strategy A permitted therapies described as glucose-dependent, including oral agents and injectable GLP-1 receptor agonists. Strategy B used glimepiride and could use basal insulin glargine as a first-line injectable; it also permitted several drugs that were available in Strategy A. The record does not establish that every participant received every permitted drug, or that participants in an arm followed one identical sequence of medicines.

The stated study duration was up to 72 weeks for each participant. The registry lists a start of 2014-02 and primary completion of 2015-10. The study status is terminated. The reason for termination is not reported in the registry record, so the status alone does not explain whether or how termination affected follow-up or interpretation.

The primary endpoint analysis population was participants who received at least one dose of study drug. The posted primary endpoint results give arm-specific participant counts of 98 for Strategy A and 93 for Strategy B. The record does not report the randomization method, allocation concealment, the planned original sample size, or the protocol’s original sample-size assumptions. It also does not report a detailed schedule of treatment adjustments or the criteria used to choose among permitted therapies.

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: Participants completed the first 24 weeks of the study at which time the study was stopped and interim analysis was triggered to assess feasibility. Treatment continued per protocol until study termination and participants discontinued at the next office study visit. Data was assessed from Baseline to last participant visit, up to 72 weeks.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants who received at least one dose of study drug.

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: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving and Maintaining Individualized Glycated Hemoglobin A1c (HbA1c) Targets Without Clinically Significant Hypoglycemia, measured over Baseline to last participant visit (up to 72 weeks).

The primary endpoint is the percentage of participants who achieved and maintained an individualized HbA1c target without clinically significant hypoglycemia, from baseline to the last participant visit, up to 72 weeks. Success is defined as not meeting the endpoint’s failure definition. Failure is based on HbA1c values above the upper limit of the participant’s target: for participants with HbA1c data beyond Week 24, it requires two consecutive values over a 12-week period starting at Week 24; for participants without later HbA1c data, it is based on the Week 24 value.

The endpoint also treats specified hypoglycemia as clinically significant. The registry definition includes severe hypoglycemia; repeated hypoglycemia that interrupts activities or sleep and is associated with blood glucose at or below 3.9 mmol/L; or repeated asymptomatic hypoglycemia associated with blood glucose below 3.0 mmol/L. Thus, the endpoint combines a measure of glycemic target maintenance with a safety condition. A participant does not count as a success merely by having HbA1c within target if the specified hypoglycemia condition is met.

Such a combined endpoint is used to represent more than glucose lowering alone: it asks whether target attainment is maintained without the defined clinically significant hypoglycemia. Because targets are individualized, the endpoint is not a comparison against one common HbA1c threshold for every participant. The record does not report the target-setting procedure or the distribution of target values.

7. Results Posted in the Registry

• Strategy A (Glucose-Dependent): 64.3% (63/98) versus 54.8% (51/93) on control; risk difference 9.4 percentage points (95% CI -4.4 to 23.3), risk ratio 1.17 (0.93–1.48); unadjusted two-proportion z-test p = 0.183.

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.

Percentage of Participants Requiring Alternative Treatment Due to Glycemic Failure of First Line Injectable Therapy

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Strategy A (Glucose-Dependent): 21.4% (21/98) versus 12.9% (12/93) on control; risk difference 8.5 percentage points (95% CI -2.1 to 19.1), risk ratio 1.66 (0.87–3.18); unadjusted two-proportion z-test p = 0.119.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Strategy A (Glucose-Dependent) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline of Urinary Albumin to Creatinine Ratio

• 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:
  • Strategy A (Glucose-Dependent): mean 1.85 versus 1.85 on control; difference 0.00 (95% CI -6.16 to 6.16), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Strategy A (Glucose-Dependent) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Body Mass Index (BMI)

• 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:
  • Strategy A (Glucose-Dependent): mean -0.47 versus 0.20 on control; difference -0.67 (95% CI -1.34 to -0.00), standardized effect d = -0.29; z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Strategy A (Glucose-Dependent) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary endpoints extend the comparison beyond the combined glycemic-control and hypoglycemia outcome. They include the need for alternative treatment after failure of first-line injectable therapy, hypoglycemia categories, urinary albumin to creatinine ratio, body mass index, and estimated glomerular filtration rate. The posted numerical details do not cover every listed outcome in the same way, and some outcome results are not reported in the registry record.

At a broad level, the secondary results address different questions rather than serving as interchangeable checks of the primary endpoint. The alternative-treatment endpoint concerns treatment escalation, while the kidney-related measures and body mass index are continuous outcomes. Hypoglycemia is relevant to the safety component of the primary endpoint, but a secondary count of hypoglycemia categories is not the same as the primary combined success definition. A participant-level relationship between these endpoints cannot be inferred from arm-level summaries.

The secondary pattern should be considered alongside, but not as a replacement for, the primary comparison. Differences in outcome definition, measurement, and available participants mean that apparent directional agreement or disagreement does not necessarily strengthen or undermine the primary estimate. In particular, the primary confidence interval includes no difference, and secondary outcomes do not remove that uncertainty.

Unadjusted secondary results carry less weight because multiple outcomes can create more opportunities for chance findings, especially when the number of planned tests and any multiplicity procedure are unknown. The registry lists no reported analyses for the posted secondary outcomes, and a statistical analysis plan is not reported. These results are most useful as descriptive context and as questions that could inform future research, rather than as stand-alone confirmatory evidence.

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

• Percentage of Participants Requiring Alternative Treatment Due to Glycemic Failure of First Line Injectable Therapy
• Number of Participants With Total Hypoglycemia and Other Categories of Hypoglycemia
• Change From Baseline of Urinary Albumin to Creatinine Ratio
• Change From Baseline in Body Mass Index (BMI)
• Change From Baseline of Estimated Glomerular Filtration Rate (eGFR)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the percentage measure?

The primary endpoint is a binary outcome at the participant level: a participant either meets the success definition or does not. The arm percentage expresses the share of participants meeting that definition. In this study, success means avoiding the specified failure of HbA1c target maintenance and avoiding clinically significant hypoglycemia as defined in the registry. A binary endpoint makes the outcome easy to summarize, but it compresses several kinds of information. It does not show how far an HbA1c value was from target, how long a participant remained in target, or which component led to failure.

The endpoint uses individualized targets, so participants may have different target limits. Its failure rule also distinguishes participants with HbA1c measurements after Week 24 from those without later HbA1c data. That rule specifies how the endpoint classifies those situations; it does not tell the reader how much data were missing, why data were missing, or whether additional missing-data methods were used. Those details are not reported in the registry record.

How should the arm comparison be read?

The risk difference compares the two arm-level probabilities of success by subtraction, with the direction stated as Strategy A relative to Strategy B. The recalculated estimate of 0.095 is positive, so the observed difference points toward a higher success probability in Strategy A. Its 95% confidence interval, -0.044 to 0.233, includes zero. In a general statistical interpretation, zero is the value corresponding to no risk difference. An interval that includes zero does not establish that the strategies are equivalent; it indicates that the posted data do not precisely distinguish a difference from no difference under this calculation.

The unadjusted p-value is 0.183. In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor does it quantify the probability that the result will replicate. Because the registry does not report a sponsor analysis or a prespecified analysis plan, this p-value should be understood as part of the unadjusted recalculation, not as a reported confirmatory test.

Why do counts and percentages both matter?

The arm percentages give a standardized view of the observed success rate, while the counts show how many participants contributed successes among the participants included in each arm’s result. Both help readers understand the scale of the evidence. Neither resolves possible issues such as incomplete follow-up, differences in baseline risk, or how treatment choices varied within the strategies. Those questions require information not reported in the registry record.

What does a confidence interval add?

In general, a confidence interval describes the range of effect estimates reasonably compatible with the data and the method used, under repeated-sampling assumptions. It communicates uncertainty around an estimate rather than only whether a p-value passes a threshold. The interval for the risk difference spans negative and positive values, so it allows for the possibility that either strategy had a higher success probability. Its width also indicates that the result does not pin down the size of the difference precisely. A confidence interval does not account automatically for unreported sources of bias, missing-data mechanisms, or deviations from the analysis plan.

What can secondary outcomes contribute?

Secondary outcomes can help characterize a strategy across other dimensions, such as the need for alternative injectable treatment, kidney-related measures, body mass index, and hypoglycemia. Their interpretation depends on how they were prespecified, how many comparisons were planned, and whether multiplicity was addressed. Those elements are not reported in the registry record. Unadjusted secondary comparisons are therefore descriptive and should not be treated as independent confirmation of the primary finding. A pattern that is directionally consistent across outcomes may be informative, but it does not replace an appropriately planned analysis.

What assumptions matter for planning calculations?

The planning illustrations use an observed effect as their starting point and examine fractions of that effect. In general, a power calculation estimates the sample size needed to have a specified chance of detecting an effect under stated assumptions if that effect is present. It is sensitive to the assumed effect size, outcome variability or event rate, significance level, allocation, and analysis method. An effect estimated from a relatively small trial may be unstable, so planning from it should not be taken as a guaranteed requirement for a future study. The record’s planning assumptions are distinct from the original design assumptions, which are not reported.

For continuous outcomes, standard deviations describe variation among participant measurements and mean differences compare arm averages. For binary outcomes, the result is framed as a difference in event probabilities. These are different scales and should not be directly compared as if they measured the same quantity. In general, over-dispersion matters when observed variability is greater than a model assumes: standard errors can be too small if extra variability is ignored. The record does not identify an over-dispersion analysis for the primary binary endpoint, so no such adjustment should be inferred.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate an effect, not whether an effect is clinically important. The primary arm-specific success estimates are 64.5% for Strategy A, with a 95% confidence interval of 54.4 to 73.4, and 54.9% for Strategy B, with a 95% confidence interval of 44.6 to 64.9. The intervals overlap. Overlap alone is not a formal test of the difference, but it gives a visual indication that each arm’s rate is estimated with uncertainty.

The more direct comparison is the recalculated risk difference of 0.095, with a 95% confidence interval from -0.044 to 0.233. The interval crosses zero, so the data are compatible with no risk difference under this unadjusted calculation. It also spans effects in both directions. This means the estimate is not precise enough to determine the direction and magnitude of the strategy contrast with confidence. The unadjusted p-value of 0.183 is consistent with that uncertainty, but the interval provides more information about the range of compatible effect estimates.

Confidence intervals are not guarantees that the true effect lies inside a particular interval, and they do not account for limitations such as possible missing data, unreported analysis choices, or bias from an open-label design. Nor does a wide interval establish that the strategies are the same. A precise conclusion about equivalence would require an appropriate design and prespecified equivalence margins, neither of which is reported in the registry record. The confidence interval is best used to describe statistical uncertainty in the posted comparison, alongside the endpoint definition, analysis population, and incomplete reporting of the statistical plan.

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 illustrations are planning calculations based on the observed effect, not the trial’s original design assumptions. The record states a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The calculations examine an effect equal to 100%, 75%, or 50% of the observed effect. For these non-time-to-event results, the figures are participants per arm, not total events. The trial’s own original sample-size justification and assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a future study to have an 80% chance of detecting the assumed effect under the stated calculation assumptions, if that effect is present. The 90% power column gives the corresponding illustration for a 90% chance. These are planning probabilities under a model, not guarantees for a particular study; departures from assumptions, missing data, and the chosen analysis can change actual performance.

The rows based on smaller fractions of the observed effect require more participants per arm. This is expected because a smaller difference is harder to distinguish from random variation when other assumptions are held fixed. The calculations use the observed estimate, which itself is uncertain, so they should be treated as illustrations for planning rather than definitive sample-size recommendations. This is not observed 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.548; treatment proportion p₁ = 0.643; average p̄ = 0.596.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6941 = 1.3603.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6908 = 0.5814.
4. n = (1.3603 + 0.5814)² / (0.0945)² = 422.5, rounded up to 423 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
p0 <- 0.548387096774194                          # control proportion
p1 <- 0.642857142857143                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2072096)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 423 (80% power), 566 (90% power)
 75% of observed effect: n per arm = 759 (80% power), 1,016 (90% power)
 50% of observed effect: n per arm = 1,722 (80% power), 2,304 (90% power)
power.prop.test: 422.5 
Simulated power at n = 423 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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

The registry record does not report a statistical analysis plan, a multiplicity adjustment, or the number of planned hypothesis tests. It lists multiple secondary outcomes, while the reported-analyses listing contains no analyses. Without knowing which outcomes and contrasts were prespecified, how many tests were planned, and what decision rules were intended, the risk of chance findings across the outcome set cannot be quantified from the record.

This matters because interpreting each unadjusted p-value as if it were the only test can overstate the strength of evidence when many outcomes are examined. Multiplicity procedures control the chance of false-positive conclusions across a defined family of tests, but the appropriate family and method depend on the study’s aims and analysis plan. No such method should be assumed for this trial. Secondary comparisons should therefore be read as exploratory or descriptive unless further documentation establishes their prespecified role and analysis.

Missing-data handling is also incompletely described. The primary endpoint definition specifies how a participant without HbA1c data beyond Week 24 is classified using the Week 24 value. That rule addresses a particular measurement situation, but the record does not report the amount or reasons for missing data, methods for other missing values, sensitivity analyses, or assumptions about participants with incomplete follow-up. The status is terminated, and the reason for termination is not reported in the registry record. The available information does not establish whether termination led to missing endpoint data or altered the planned analysis.

The primary endpoint population is described as participants who received at least one dose of study drug. The record does not report an intention-to-treat analysis, the number randomized to each arm, or a comparison between randomized and treated populations. It also does not report how protocol deviations, treatment discontinuation, or changes in permitted medicines were handled analytically. These omissions limit assessment of how closely the posted results preserve the benefits of randomization and how robust the results are to alternative population definitions.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: atrial fibrillation (2.2%), myocardial infarction (2.2%), cerebrovascular accident (2.0%), cardiac failure congestive (1.1%), lower gastrointestinal haemorrhage (1.1%).

The registry reports participants with serious adverse events in each treatment strategy: 15 of 98 in Strategy A and 14 of 93 in Strategy B. It also reports other adverse events for 82 of 98 in Strategy A and 74 of 93 in Strategy B. These figures describe participants recorded in the event categories; they do not give event duration, severity beyond the serious classification, timing, or a causal assessment for each event. The registry does not report deaths in the posted safety figures.

The listed serious adverse event terms include atrial fibrillation and myocardial infarction at 2.2% each, cerebrovascular accident at 2.0%, cardiac failure congestive at 1.1%, lower gastrointestinal haemorrhage at 1.1%, and appendicitis at 1.1%. The record does not give enough detail in these listings to infer a comparative risk for each event term or attribute an event to a treatment strategy.

These summaries are descriptive safety information, not proof that one strategy is safer. The arm sizes and follow-up, the event definitions, and the absence of a reported causal analysis should be considered. No medical conclusion should be drawn from comparing these counts alone.

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

The posted primary results show that the observed percentage meeting the combined individualized HbA1c and hypoglycemia success definition was higher in Strategy A than in Strategy B. The unadjusted recalculated comparison points in that same direction, but its confidence interval includes zero and spans both negative and positive differences. The result therefore does not establish a clear difference between strategies, and it does not establish that the strategies are equivalent.

The endpoint represents a specific combination of target maintenance and avoidance of defined clinically significant hypoglycemia over follow-up up to 72 weeks. It does not, by itself, describe average HbA1c change, the frequency of every type of hypoglycemia, the burden of treatment, quality of life, or long-term complications. Nor does an arm-level percentage show which individual participants experienced the different outcome components.

The comparison is between treatment strategies with overlapping permitted medications, rather than between two single medicines. Investigator choice and the treatment options allowed within each arm mean that the result cannot be attributed to one particular drug from the registry information. The open-label design and the lack of reported analysis details also matter when assessing the strength of the evidence.

The findings apply to the recorded study population and endpoint definition; the registry does not provide enough information to establish how broadly they generalize to other populations or care settings. The status is terminated, and its reason and implications are not reported. Overall, the posted result is an uncertain descriptive comparison, not a basis for medical advice or a definitive claim that either strategy works better or worse.

17. Why This Trial Matters Statistically

This trial illustrates why the choice of endpoint matters in clinical research. A binary success measure that combines individualized glycemic targets with avoidance of specified hypoglycemia captures more than glucose lowering alone, but it also combines distinct clinical experiences into one result. Readers need the endpoint definition to understand what an arm percentage represents and what it leaves out.

It also illustrates the value of distinguishing an estimate from its precision. The direction of the observed primary difference favors Strategy A, but the unadjusted confidence interval includes zero and permits effects in either direction. Reporting only the arm percentages or a single p-value would give a less complete view of the uncertainty. The interval makes clear that the posted data do not precisely determine the size of the strategy contrast.

Strategy-level trials can be difficult to interpret when arms permit multiple medications and choices vary by participant. The randomization compares assigned strategies, not isolated drug effects. A reader should not treat the result as a direct test of any individual medicine unless a separate analysis supports that conclusion.

Finally, the record highlights the importance of transparent reporting of analysis plans, missing-data handling, multiplicity, and reasons for trial termination. Those details help distinguish confirmatory analyses from exploratory comparisons and clarify how much confidence to place in observed patterns. Their absence does not erase the posted data, but it limits the conclusions that can be drawn from them.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations specific to this record constrain interpretation. The study is open-label, so participants and investigators were not masked to assigned strategy. The primary outcome includes an HbA1c component and a hypoglycemia component; the record does not report separate primary-component results that would show which part drove success or failure. Target setting is individualized, but the target-setting procedure and target distributions are not reported.

The trial compared flexible strategies with overlapping permitted therapies. The registry does not report which medicines participants actually received, treatment sequences, adherence, or the extent of treatment changes. Therefore, the posted strategy comparison cannot identify the effect of a particular drug or explain how variation in treatment contributed to the result.

The registry status is terminated, but the reason and consequences are not reported. It is consequently not possible to determine from this record whether planned follow-up was completed or whether termination affected outcome availability. Missing-data amounts, reasons, and sensitivity analyses are also not reported. The primary endpoint rule for participants without HbA1c data beyond Week 24 is specified, but that alone does not resolve other missing-data questions.

The record does not report the original sample-size rationale, the randomization details, the statistical analysis plan, multiplicity procedures, or a sponsor-reported analysis. The unadjusted comparison is therefore limited to the posted summaries and should not be mistaken for a complete confirmatory analysis. Finally, the registry information does not provide enough detail to judge representativeness beyond the stated older population with type 2 diabetes or to assess the clinical importance of the estimated difference.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Comparison of Two Treatment Strategies in Older Participants With Type 2 Diabetes Mellitus (T2DM) — NCT02072096.
• Registry record last updated 2019-10-09; status last verified 2019-09.
• Results first posted 2016-11-23.
• 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

IMPERIUM is recorded as a Phase 4, randomized, open-label, parallel-group comparison of a glucose-dependent treatment strategy and a reference strategy in older participants with type 2 diabetes. The registry lists 192 for enrollment, a study duration of up to 72 weeks per participant, and a terminated status. The reason for termination is not reported in the registry record.

The primary endpoint was success in achieving and maintaining individualized HbA1c targets without clinically significant hypoglycemia. Posted success percentages were 64.5% for Strategy A and 54.9% for Strategy B. The unadjusted recalculated risk difference was 0.095, with a 95% confidence interval from -0.044 to 0.233 and p = 0.183. The interval includes zero, leaving substantial uncertainty about the direction and size of the difference.

The registry does not report a statistical analysis plan, original sample-size assumptions, multiplicity handling, or detailed missing-data analyses. Secondary and safety findings offer additional descriptive context, but do not resolve the uncertainty in the primary comparison.