Automated Insulin Delivery in Elderly With Type 1 Diabetes (AIDE T1D): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Automated Insulin Delivery in Elderly With Type 1 Diabetes (AIDE T1D) (NCT04016662), a randomized phase 4 study. The primary outcome is CGM Measured Time <70 mg/dL.

2. Clinical Question

The clinical question is framed around time spent below a glucose threshold, an indicator of exposure to low sensor glucose. The registry also lists other glucose measures, hypoglycemia events, and HbA1c as secondary outcomes. The comparisons describe posted results for each treatment condition; they do not by themselves establish how an individual would respond in routine care.

The crossover structure means that participants used each of the three approaches in sequential periods. The registry describes a run-in phase with training on study devices before the crossover, followed by an opportunity to use a study device after the crossover. The primary endpoint uses data from weeks 5-12 of each 12-week intervention period. The first 4 weeks of each period were excluded from this endpoint to reduce the chance of carryover effects.

3. Trial Design

The registry identifies this as a randomized, unmasked, phase 4, crossover trial, with enrollment of 82 and a completed status. It evaluated three conditions: HCL with Tandem t:slim X2 Control-IQ technology and Dexcom G6; PLGS with Tandem t:slim X2 Basal-IQ technology and Dexcom G6; and SAP therapy with the HCL and PLGS features turned off, also using Dexcom G6.

The trial consisted of a run-in phase followed by three sequential 12-week treatment periods. During the run-in, participants received training using the study devices. Each participant was assigned to use HCL during one period, PLGS during one period, and SAP during one period. The registry describes randomization but does not report the randomization sequence details, any washout procedure, or the statistical approach used to account for treatment order or within-participant correlation.

For the primary endpoint, the registry specifies weeks 5-12 of each intervention period. The initial 4 weeks were not included in the endpoint calculation because of the stated concern about carryover. A minimum of 168 hours of sensor data was required to calculate continuous glucose monitoring metrics. After the final crossover period, participants could use study devices for an additional 12 weeks. That optional period was intended to assess system preference and related characteristics, durability, and safety in a setting with less frequent study contact; it is not the timeframe for the primary endpoint.

The registry lists 15 outcome measures and reports results for the primary outcome and a selection of secondary outcomes. It does not report the trial’s original sample-size justification, planned statistical model, detailed allocation procedures, or an analysis population definition. Those details are not reported in the registry record, so the posted summary statistics should not be read as a complete account of the trial protocol or analysis.

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: This was a crossover study, so the same 82 randomized patients participated in each arm. If they drop out, they might not be in one of the arms.

Run-In Phase

Reasons for not completing this period:

HCL (12 Weeks)

Reasons for not completing this period:

PLGS (12 Weeks)

Reasons for not completing this period:

SAP (12 Weeks)

Reasons for not completing this period:

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: The same 82 patients at baseline participated in each arm unless they dropped or there was a death.

6. Primary Endpoint

The registry lists the primary outcome as CGM Measured Time <70 mg/dL, measured over weeks 5-12 of 12 weeks for each intervention of the crossover.

The primary endpoint is continuous glucose monitoring measured time below 70 mg/dL, expressed as a percentage of sensor glucose values. It describes the share of recorded sensor readings that fell under the specified threshold during weeks 5-12 of each 12-week intervention period. The registry reports the endpoint as a mean with a standard deviation for each treatment condition.

Time below a threshold is useful because it summarizes the duration of low sensor glucose exposure across a monitoring period. Unlike a single glucose measurement, it reflects readings collected over time. It is also distinct from a count of hypoglycemic events: the percentage of time below 70 mg/dL measures sensor-data exposure, while an event outcome records the frequency of events according to the trial’s definition. The registry record does not give further detail on the event definition.

The first 4 weeks of each intervention period were excluded from this endpoint to reduce the chance of a carryover effect from the preceding treatment condition. The calculation also required at least 168 hours of sensor data. The registry notes that hypoglycemia endpoints had skewed distributions and that values were winsorized at the 10th and 90th percentiles. Winsorization limits the influence of unusually low or high observations by replacing values beyond specified cutoffs with values at those cutoffs; it does not mean that every observation was removed.

These choices describe how the registry says the endpoint was constructed. The specific analysis model, handling of missing sensor data beyond the minimum-data rule, and any adjustment for crossover sequence are not reported in the registry record.

7. Results Posted in the Registry

• Predictive Low-Glucose Insulin Suspension (PLGS): mean 1.67 versus 1.58 on control; difference 0.09 (95% CI -0.21 to 0.39), standardized effect d = 0.09; z-test p = 0.551.
• Sensor-Augmented Pump (SAP): mean 2.57 versus 1.58 on control; difference 0.99 (95% CI 0.59 to 1.39), standardized effect d = 0.78; 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.

CGM Measured Time <54 mg/dL

• 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:
  • Predictive Low-Glucose Insulin Suspension (PLGS): mean 0.27 versus 0.29 on control; difference -0.02 (95% CI -0.09 to 0.05), standardized effect d = -0.09; z-test p = 0.557.
  • Sensor-Augmented Pump (SAP): mean 0.48 versus 0.29 on control; difference 0.19 (95% CI 0.09 to 0.29), standardized effect d = 0.59; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Predictive Low-Glucose Insulin Suspension (PLGS) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Sensor-Augmented Pump (SAP) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Hypoglycemia

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Predictive Low-Glucose Insulin Suspension (PLGS): 0.50 versus 0.60 (hypoglycemic events per week) on control; rate ratio 0.83 (95% CI 0.35–2.00, approximate, Poisson model); p ≈ 0.683.
  • Sensor-Augmented Pump (SAP): 0.90 versus 0.60 (hypoglycemic events per week) on control; rate ratio 1.50 (95% CI 0.70–3.22, approximate, Poisson model); p ≈ 0.297.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Predictive Low-Glucose Insulin Suspension (PLGS) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Sensor-Augmented Pump (SAP) and the control. The interval gives the range of effects that remain compatible with the data.

Glucose Control

• 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:
  • Predictive Low-Glucose Insulin Suspension (PLGS): mean 161.00 versus 152.00 on control; difference 9.00 (95% CI 2.85 to 15.15), standardized effect d = 0.46; z-test p = 0.004.
  • Sensor-Augmented Pump (SAP): mean 160.00 versus 152.00 on control; difference 8.00 (95% CI 2.36 to 13.64), standardized effect d = 0.44; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Predictive Low-Glucose Insulin Suspension (PLGS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Sensor-Augmented Pump (SAP) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several aspects of glucose monitoring and control: time below a lower glucose threshold, hypoglycemic events, glucose concentration, time in and above ranges, coefficient of variation, and HbA1c. The posted results therefore offer a broader descriptive picture than the primary endpoint alone. The available secondary results include measures whose comparison patterns are not all the same, and their scales differ. They should be interpreted outcome by outcome rather than combined into a single overall conclusion.

At a broad level, some posted continuous measures show a pattern similar to the primary comparison of HCL with SAP, while comparisons of HCL with PLGS are less clearly separated on some low-glucose measures. Event-rate comparisons have wide intervals that include the null rate ratio. These cross-endpoint patterns can help readers understand whether the primary result appears isolated or occurs alongside related measures. They cannot establish a unified treatment effect, because each outcome measures something different and the registry does not report a prespecified hierarchy or a comprehensive analysis plan.

Secondary results generally carry less inferential weight than a primary endpoint when many outcomes or comparisons are examined. Each additional test creates another opportunity for a result to appear noteworthy by chance. Adjustment methods or a prespecified testing sequence can address this issue, but a multiplicity procedure is not reported in the registry record. The secondary p-values are therefore unadjusted, and should be treated as exploratory evidence rather than definitive independent confirmations.

The registry lists 15 outcome measures, while results are posted for 9 secondary outcomes. The record does not explain why the other listed secondary measures lack posted results. Missing results do not establish that an outcome was not measured or that its result was unfavorable. They do, however, mean that the reported secondary pattern may not represent every outcome listed in the registry. The complete protocol and analysis plan are not reported in the registry record, limiting assessment of selective reporting and the intended role of each secondary endpoint.

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

• CGM Measured Time <54 mg/dL
• Hypoglycemia
• Glucose Control
• % Time 70-180 mg/dL
• Glucose Control - Coefficient of Variation
• % Time > 180 mg/dL
• % Time > 250 mg/dL
• HbA1c

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure reported as a mean and standard deviation. The mean describes the average percentage of sensor readings below the threshold in each condition. The standard deviation describes spread among the values around that average. A standard deviation is not the same as the uncertainty in the estimated mean: uncertainty in a treatment comparison is more directly conveyed by its confidence interval.

What does a mean difference represent?

A mean difference compares the average outcome in one condition with the average in the reference condition. The posted comparisons use HCL as the reference. For PLGS, the estimated difference is 0.09; for SAP, it is 0.99. Because the outcome is percentage of time below 70 mg/dL, these are differences on that endpoint’s reported scale. They are not relative changes or ratios. A positive estimate means the compared condition’s mean is higher than the HCL mean in the posted summary.

The reported arm means and standard deviations are useful descriptive information, but a crossover trial has a feature that a simple parallel-group comparison does not: participants contribute experience under more than one condition. A full crossover analysis may account for the association between measurements from the same participant, as well as treatment period and sequence. The registry record does not report the model or its treatment of these features. The unadjusted summary-statistic comparisons cannot reveal the within-participant covariance or establish that the trial’s formal analysis used the same calculation.

Why use a confidence interval?

A confidence interval communicates uncertainty around an estimate by giving a range of values compatible with the analysis and its assumptions. It is not a range containing a fixed proportion of individual participants’ outcomes, and it does not give the probability that the true effect lies in the interval. For the PLGS comparison, the posted interval runs from -0.206 to 0.386 and includes zero. For the SAP comparison, the interval has positive limits. These patterns describe the precision and direction of the estimates under the comparison method; they do not resolve limitations in the analysis plan or multiple testing.

A p-value describes how incompatible the observed data are with a specified null model, assuming the analysis assumptions hold. The registry lists unadjusted p-values of 0.551 for PLGS versus HCL and <0.001 for SAP versus HCL. An unadjusted p-value does not account for testing multiple endpoints or comparisons unless that adjustment is built into the analysis. The record does not report a multiplicity procedure, so the p-values should not be treated as if such an adjustment had been made.

What does winsorization do?

The registry says that the hypoglycemia endpoints had skewed distributions and that values were winsorized at the 10th and 90th percentiles. Skewness means values are not distributed symmetrically around a central value; a small number of extreme observations can have substantial influence on a mean. Winsorization reduces the influence of extremes by setting values beyond the selected cutoffs to the cutoff values. It differs from deleting those observations. The record does not provide a sensitivity analysis using unmodified values, so the effect of this procedure on the estimates cannot be assessed from the registry summary.

The minimum-data requirement of 168 hours makes clear that some amount of sensor data was needed to calculate the monitoring metrics. The registry does not report how many records met that requirement for each period, how missing readings were handled, or whether other missing-data methods were used. The reported mean and standard deviation therefore cannot show whether missingness differed by treatment condition or whether it affected the comparison.

How should event-rate comparisons be read?

Some secondary outcomes are event rates rather than continuous glucose measures. The registry reports hypoglycemic events per week and comparisons as rate ratios. A rate ratio compares event rates proportionally: a value of 1 would represent equal rates under the stated calculation, while a value below or above 1 indicates a lower or higher rate in the compared condition. The posted estimate for PLGS versus HCL is 0.833, with an interval from 0.347 to 2.0; for SAP versus HCL it is 1.5, with an interval from 0.700 to 3.216. Both intervals include 1, and the unadjusted p-values are 0.683 and 0.297. The registry indicates a Poisson-based calculation for these comparisons, but does not report a complete model or any adjustment for extra-Poisson variation. In general, over-dispersion occurs when event counts vary more than a basic Poisson model expects; ignoring it can affect standard errors and inference. Whether this issue affected the trial analysis is not reported in the registry record.

Other continuous outcomes are summarized with means and standard deviations, including glucose control in mg/dL and time below 54 mg/dL. These outcomes have their own scales and clinical interpretations; their estimates should not be directly compared with the primary endpoint’s percentage scale. Together, the measures offer different descriptions of glucose exposure and control, but the registry’s brief result summaries do not replace the full protocol, statistical analysis plan, or publication-level reporting.

11. Confidence Intervals and Precision

Precision is best considered through both the size of an estimate and the span of its confidence interval. For the primary endpoint, PLGS versus HCL has an estimated mean difference of 0.09, with an interval from -0.206 to 0.386. The interval crosses zero, so the posted comparison is compatible with a difference in either direction as well as with little difference. Its range is broad relative to the point estimate, indicating that the estimate is not precise enough to pin down a narrow set of values.

For SAP versus HCL, the estimated mean difference is 0.99 and the interval has a positive lower bound and an upper bound of 1.39. The interval excludes zero, but still spans a range of possible effect sizes. The posted summaries thus distinguish the pattern of this comparison from the PLGS comparison, without making the magnitude certain at a fine level. A p-value such as <0.001 does not make an estimate more precise; the confidence interval is the more direct indication of its uncertainty.

These intervals accompany unadjusted summary-statistic comparisons, not a fully documented crossover model. The registry does not report whether the trial’s formal analysis accounted for participant-level pairing, treatment period, or treatment sequence. Nor does it provide a reported analysis population or detailed missing-data analysis. Those omissions limit how confidently these intervals can be interpreted as inferential results for the trial’s intended analysis.

Standard deviations of 0.95, 0.96, and 1.54 for the primary outcome describe the dispersion of values within conditions. They are not measures of precision for the mean difference. Precision also depends on the amount of information and the analysis structure, including correlations in a crossover trial. The registry summary does not report all information needed to assess that structure.

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 the trial’s original design assumptions. They show participants per arm for the continuous and rate comparisons in this record; none of these comparisons is a time-to-event outcome requiring a total event count. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set as the stated fraction of the observed effect. The trial’s own original sample-size justification is not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a future study to have an 80% chance of detecting the chosen effect under those assumptions, if the assumptions and effect are correct. The 90% power column gives the corresponding planning number for a 90% chance. Greater planned power generally requires more participants when other assumptions are unchanged. The rows that plan for 75% or 50% of the observed effect use smaller effects than the row based on the full observed effect. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm.

These calculations are not observed power for the completed trial. They do not establish that the trial was adequately or inadequately sized, and they should not be used as a substitute for a protocol-based design calculation. Observed effects can be uncertain and may not match the effect a future study considers important. The planning curve should be read as illustrating how required sample size changes across the stated effect assumptions, not as a prediction that a future trial will obtain a particular result.

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 = 0.090; pooled standard deviation σ = 0.955.
2. n = 2 × (1.96 + 0.842)² × 0.955² / 0.090² = 1,767.3, rounded up to 1,768 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 <- 0.0899999999999999                      # observed difference in means
sigma <- 0.954949796546421                     # 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(4016662)
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 = 1,768 (80% power), 2,366 (90% power)
 75% of observed effect: n per arm = 3,142 (80% power), 4,207 (90% power)
 50% of observed effect: n per arm = 7,070 (80% power), 9,464 (90% power)
power.t.test: 1768.3 
Simulated power at n = 1,768 per arm: 0.804 (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

The registry lists 15 outcome measures and posts 9 secondary outcomes. It does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a prespecified sequence that would control the chance of false-positive findings across the analyses. The posted comparison p-values are unadjusted. When many outcomes and pairwise comparisons are considered, an unadjusted p-value for one result does not account for the broader set of opportunities to observe a small p-value. This is a reason to give secondary results less weight, not proof that any particular result is false.

The registry record also does not report the detailed analysis plan, including the model for the randomized crossover structure, treatment sequence, period effects, or participant-level correlation. Randomization and crossover are stated design features, but their presence alone does not show how they were incorporated into the reported statistical analysis. The registry does not report a defined analysis population or enough participant-flow detail to determine which population contributed to each endpoint result.

Missing-data handling is only partly described. The primary continuous glucose metrics required a minimum of 168 hours of data, and the first 4 weeks of each intervention period were excluded to reduce potential carryover. Beyond these endpoint rules, the handling of missing sensor values, incomplete periods, or missing secondary outcomes is not reported in the registry record. The number of participants contributing to the posted endpoint summaries differs across treatment conditions, but the registry does not explain the reasons for this or describe a missing-data sensitivity analysis.

The record’s listed analysis count is 0, and it does not include registered analysis records. This should not be taken to mean that no analyses were conducted: numerical results are posted. Rather, the registry does not document the analyses in a way that permits a full comparison with a prespecified statistical plan. Details about interim analyses, stopping rules, covariate adjustment, and multiplicity are not reported in the registry record.

These gaps matter because registry summary results are not a substitute for the full protocol and statistical analysis plan. Without those documents, it is not possible to determine which analyses were planned in advance, how deviations were handled, or whether the posted results represent every intended analysis.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypoglycemia (2.6%), diabetic ketoacidosis (2.5%), severe hypoglycemia (1.3%), peripheral arterial disease (1.3%), intracranial hemorrhage (1.3%).

The registry reports serious adverse events by phase or treatment condition, with the number at risk and the number affected. In the run-in phase, 2 of 105 were affected by serious adverse events, and 1 death was reported. For HCL, 8 of 81 were affected and no deaths were reported. For PLGS, 3 of 79 were affected and 1 death was reported. For SAP, 3 of 78 were affected and 1 death was reported. These are registry counts for the stated groups; they should not be added together because the trial used a crossover design and the groups represent phases or conditions.

The registry also lists serious-event terms and percentages, including hypoglycemia at 2.6%, diabetic ketoacidosis at 2.5%, severe hypoglycemia at 1.3%, peripheral arterial disease at 1.3%, intracranial hemorrhage at 1.3%, and hyperglycemia at 1.2%. The record does not provide enough detail in these summaries to establish how events were attributed across treatment periods or to compare event risk causally. Adverse-event counts describe reported safety observations; they do not by themselves establish that a treatment caused an event or that an event was absent when no count is listed.

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

The posted results describe outcomes observed during a randomized crossover trial of HCL, PLGS, and SAP in older adults with type 1 diabetes. For the primary measure, the mean percentage of sensor glucose values below 70 mg/dL was 1.58 with HCL, 1.67 with PLGS, and 2.57 with SAP. The unadjusted summary comparison of PLGS with HCL is imprecise and includes zero in its interval; the comparison of SAP with HCL has a positive interval. This states what the posted summaries show, without turning the estimates into treatment advice or a conclusion about what any individual should use.

The registry result does not establish that one approach works or does not work. Statistical evidence about a group average is not the same as a guaranteed individual response. The record does not report a clinically important difference threshold for the primary endpoint, so it is not possible to judge from these results alone whether the estimated difference is large enough to matter clinically. Nor does a small p-value answer that question: it addresses compatibility with a null model under assumptions, not the practical importance of an effect.

The study’s crossover design can support comparisons within participants, but the registry does not report enough of the formal analysis to determine how that structure was handled. The summary-statistic comparisons do not make use of participant-level paired information in a way that can be verified from the posted figures. The absence of a reported multiplicity approach, detailed missing-data methods, and complete secondary results further limits interpretation.

The findings apply to the trial’s measured outcomes and timeframes. The primary endpoint uses weeks 5-12 of each intervention period, following the stated exclusion of the first 4 weeks, and requires a minimum of 168 hours of sensor data. The additional use period after the crossover was described as an opportunity to assess preference, durability, and safety, but its results are not included in the numerical summaries. Broader claims about long-term outcomes, daily experience, or populations beyond the trial are not established by these registry results.

17. Why This Trial Matters Statistically

This trial is statistically informative because it uses a randomized crossover design to compare three technology conditions in the same study population. The central methodological opportunity in a crossover trial is that each participant can contribute observations under multiple conditions. That structure can make within-person comparisons valuable, but it also requires analysis that accounts for repeated observations, treatment periods, and possible carryover. The registry describes excluding the first 4 weeks from the primary endpoint to reduce carryover, while leaving the formal analysis model unreported.

The endpoint also illustrates why outcome definition matters. Percentage of sensor readings below 70 mg/dL is not interchangeable with event counts, glucose concentration, time in range, or HbA1c. Each captures a different dimension of glucose monitoring and control. Looking across endpoints can help frame the primary result, but it cannot replace a prespecified outcome hierarchy or an analysis plan that explains how evidence across measures should be interpreted.

Precision is important alongside statistical significance. The PLGS comparison has an interval that includes zero and permits a range of possible differences; the SAP comparison has an interval with positive limits. These distinctions are more informative than treating a p-value as a simple pass-or-fail result. At the same time, all posted comparisons need to be read with the limitations of unadjusted summary analyses and unreported multiplicity procedures in mind.

The registry provides useful design and outcome details, including the monitoring timeframe, data minimum, and treatment configurations. It does not report the original sample-size justification or the analysis plan needed to fully assess the reported inference. The case therefore highlights a broader statistical lesson: a clear endpoint and a randomized design are important, but transparent reporting of planned analyses, missing-data methods, and crossover modeling is also essential for judging how strongly results support a conclusion.

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 specific to this trial affect interpretation of the posted results. First, although the registry identifies a randomized crossover design, it does not report how the analysis handled participant-level pairing, treatment sequence, period effects, or carryover. Excluding the first 4 weeks of each period was intended to reduce the chance of carryover for the primary endpoint, but the registry does not report whether other analyses or sensitivity checks addressed this issue.

Second, the registry identifies the trial as unmasked. It does not report whether this was considered in outcome assessment or how possible behavioral effects were addressed. The primary outcome is based on sensor data, but choices about device use, adherence, and missing readings can still affect the availability and interpretation of measurements. Further detail is not reported in the registry record.

Third, the outcome calculation required at least 168 hours of data, but the record does not explain how participants or periods with insufficient data were handled, or whether missingness differed across conditions. The analysis population and participant flow for each endpoint are not reported. The mean and standard deviation summaries alone cannot resolve these questions.

Fourth, hypoglycemia endpoints were winsorized at the 10th and 90th percentiles because their distributions were skewed. The registry does not report sensitivity analyses with a different distributional approach or without winsorization. It also does not provide enough detail about event definitions or the event-rate model to evaluate all modeling assumptions.

Finally, the registry does not report a multiplicity procedure or the original sample-size rationale, and only 9 secondary outcomes have posted results despite 15 outcome measures being listed. The record does not explain the status of the other outcomes. These reporting gaps limit assessment of selective reporting, precision, and the intended confirmatory role of the secondary findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Automated Insulin Delivery in Elderly With Type 1 Diabetes (AIDE T1D) — NCT04016662.
• Registry record last updated 2025-01-15; status last verified 2024-12.
• Results first posted 2025-01-15.
• 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 a completed, randomized, unmasked, phase 4 crossover trial with enrollment of 82. Participants used HCL, PLGS, and SAP in sequential 12-week periods after a device-training run-in. The primary endpoint was percentage of sensor glucose values below 70 mg/dL during weeks 5-12 of each period, with the first 4 weeks excluded to reduce potential carryover.

Posted means were 1.58 for HCL, 1.67 for PLGS, and 2.57 for SAP. The unadjusted summary comparison of PLGS with HCL was 0.09, with an interval that includes zero; the SAP comparison was 0.99, with an interval above zero. These comparisons describe the posted summaries and do not replace a full crossover analysis.

The registry does not report the detailed analysis plan, multiplicity approach, original sample-size justification, or complete missing-data methods. Secondary and safety results add context but require cautious interpretation in light of these reporting limitations.