Evaluation of The Postprandial Impact of Automated Priming Bolus for Full Closed Loop Insulin Delivery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of The Postprandial Impact of Automated Priming Bolus for Full Closed Loop Insulin Delivery (NCT05528770), a randomized na study. The primary outcome is Difference in Daytime Percent Time-in-range.

2. Clinical Question

3. Trial Design

This was a randomized, unmasked, crossover study of full closed-loop insulin delivery with versus without a Bolus Priming System. The registry identifies the study phase as NA and the status as completed. The listed enrollment is 15. The study dates recorded in the registry are 2022-10-20 for the start and 2023-01-13 for primary completion.

The two sequence descriptions specify full closed-loop delivery with BPS followed by delivery without BPS, or the reverse order. Each description refers to two separate 24-hour periods. The text about what separates those periods is truncated in the registry record, so the interval and any washout procedure are not reported in the registry record. The record also does not report how the treatment sequence was generated or concealed.

A crossover design exposes participants to both conditions, so each person can potentially contribute information under each condition. In general, this can reduce the influence of stable differences between people when the analysis accounts for the paired observations. The registry's posted primary outcome summaries list 11 observations for each condition, but do not identify whether those observations are paired or explain how the crossover structure was handled in the analysis.

The study's stated purpose was to understand the impact of automated priming boluses on safety and feasibility of a fully automated controller. The primary endpoint posted in the results is daytime percentage of CGM values in range. The registry does not provide a detailed feasibility endpoint in the registry record reported for this record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 15 participants signed informed consent for the main study. 2 screen failed and 2 withdrew prior to randomization to arms. Results reported on 11 participants who were randomized.

Overall Study

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 Difference in Daytime Percent Time-in-range, measured over 18 hours.

The primary endpoint is the percentage of continuous glucose monitoring (CGM) values that fell between 70 and 180 mg/dL during daytime, defined as 6am to midnight. The registry gives the timeframe as 18 hours and identifies the outcome as a mean with standard deviation. In practical statistical terms, the endpoint summarizes how much of the recorded daytime glucose profile was within the specified range.

Time in range is a continuous measure: it can take different values across a spectrum rather than simply classifying a participant as having or not having an event. Reporting the mean describes the group's average percentage, while the standard deviation describes variation among the observations. Neither summary alone conveys the full distribution or the within-person change across the crossover conditions.

As a general measurement concept, a target-range summary can express glucose exposure over a period in a way that is more informative than a single reading. The endpoint is relevant to the study's postprandial question because meals and the priming system are intended to affect glucose patterns over time. However, this outcome aggregates daytime CGM values; it does not isolate a particular meal response. The registry's primary endpoint does not by itself measure safety or establish whether the controller was feasible to use.

7. Results Posted in the Registry

• FCL Without BPS: mean 65.10 versus 67.40 on control; difference -2.30 (95% CI -16.41 to 11.81), standardized effect d = -0.14; z-test p = 0.749.

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.

Difference in Overall Percent Time-in-range

• 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:
  • FCL Without BPS: mean 73.10 versus 74.30 on control; difference -1.20 (95% CI -13.70 to 11.30), standardized effect d = -0.08; z-test p = 0.851.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FCL Without BPS and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary outcomes: overall time in range, daytime time below range, and overall time below range. It posts a detailed summary for overall time in range, but detailed estimates for the two time-below-range outcomes are not reported in the registry record. The available secondary information therefore gives an incomplete picture of the full prespecified or registered outcome set.

For overall time in range, the posted group means are close, and the unadjusted interval is broad and includes zero. This general pattern is consistent with the primary endpoint in that the posted summaries do not provide a precise estimate of a difference. The outcomes are not identical, however: the primary endpoint is daytime time in range, while overall time in range covers a 24-hour timeframe. The secondary measures of time below range address a different part of the glucose profile.

Secondary outcomes can help describe whether a pattern appears across related measures, but they should not be treated as independent confirmation when many outcomes are examined. In general, testing multiple outcomes increases the chance that at least one result may appear notable by chance. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Any unadjusted secondary findings therefore carry less weight than a prespecified primary analysis, particularly when outcome estimates are incomplete or uncertainty is substantial.

The secondary outcomes add context to the kinds of glucose patterns the study intended to assess, but the registry record does not support a comprehensive comparison across all of them. No inference about the unreported time-below-range results should be made from the listed outcome names alone.

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

• Difference in Overall Percent Time-in-range
• Difference in Daytime Percent Time-below-range
• Difference in Overall Percent Time-below-range

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and the registry reports group means and standard deviations. A mean is the arithmetic average of the outcome observations. A standard deviation describes how dispersed those observations are around the mean; it is not the uncertainty in the mean itself. The uncertainty in an estimated contrast is represented by its standard error and, commonly, a confidence interval.

The posted recalculation compares the mean for FCL without BPS with the mean for FCL with BPS. It uses the group summaries to estimate an unadjusted mean difference and its confidence interval. In general, an unadjusted comparison does not account for covariates or design features unless they are explicitly incorporated. Here, the study is crossover, but the recalculation uses the posted group means and standard deviations rather than a reported within-participant covariance or paired-difference summary. The registry does not report enough information to determine how the pairing was incorporated into the sponsor's analysis.

A crossover analysis can use the fact that each participant experiences both conditions. In general, the within-person contrast can be more precise than treating observations from the conditions as independent, because stable participant-level characteristics may affect both measurements. This advantage depends on having and appropriately analyzing the paired observations. Period effects, order effects, carryover, and missing observations can also matter in crossover studies. Whether and how these features were assessed is not reported in the registry record.

The registry's sponsor analysis is described as a two-sided t-test with the parameter “Mean Difference (Final Values).” A t-test evaluates a mean contrast relative to its estimated uncertainty under the model used. A two-sided test considers departures in either direction. The record does not give the full model specification, confirm whether the test was paired, describe any adjustment for order or period, or state how missing outcome measurements were handled. The reported analysis is therefore identifiable by its stated test and result, but its assumptions and implementation cannot be fully assessed from the registry record.

A confidence interval gives a range of estimates compatible with the data and the statistical model at the stated confidence level. It is not a guarantee that the true effect lies in the realized interval, nor does it assign probability to particular values after observing the data. For a mean difference, an interval containing zero indicates that the data are compatible with no mean difference under that analysis, while also potentially allowing effects in either direction. The width conveys precision: broader intervals leave more uncertainty about the magnitude.

The unadjusted p-value and confidence interval are linked through the same general inferential framework, but they answer different questions. The p-value summarizes compatibility with a null hypothesis; the interval displays a range of effect sizes compatible with the data and model. Neither statistic resolves whether the observed range is important in practice. The registry does not report a clinically important threshold for this endpoint, so a clinical interpretation of the difference cannot be made from statistical significance alone.

In general, small groups can lead to imprecise estimates, especially when outcomes vary across observations. Here, standard deviations are reported for both conditions, and the recalculation uses a pooled standard deviation. That pooled quantity supports the unadjusted calculation but does not recover the correlation between paired crossover measurements. Because that correlation is not reported, a paired standard error cannot be independently reconstructed from these summaries.

The sponsor's reported estimate and the simple recalculation should not be treated as interchangeable. The sponsor reports a two-sided t-test of final values, while the recalculation is an unadjusted computation from the posted group summaries. The registry does not explain the differences in the estimate or analysis definition. The reported sponsor analysis remains the trial's own stated analysis; the recalculation serves as a separate descriptive check, not as evidence that the sponsor analysis was reproduced.

General statistical concepts such as confidence intervals and t-tests explain how results are commonly interpreted, but they do not fill gaps in the registry record. The original analysis plan, handling of missing data, analysis populations, crossover-specific model, multiplicity strategy, and trial's own sample-size assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The unadjusted recalculated mean difference for daytime time in range is -2.3 percentage points, with a 95% confidence interval from -16.41 to 11.81. Because this interval spans zero and extends in both directions, it is compatible with a lower mean under no BPS and with a higher mean under no BPS. The interval is broad relative to the point estimate, so the observed data do not pin down the magnitude or direction precisely.

The sponsor's reported analysis gives a mean difference of 2.23, with a 95% confidence interval from -3.8 to 8.3. That interval also includes zero and allows estimates in either direction. The point estimate and interval belong to the sponsor's stated analysis and are not the same as the recalculated contrast from the group summaries. The registry does not explain how the analysis definitions relate.

In general, a confidence interval reflects both the variability in the data and the amount of information available under the analysis model. A wide interval signals limited precision; it should not be read as evidence that every effect within it is equally plausible or clinically important. The registry does not report a threshold for a meaningful change in daytime time in range, so the clinical importance of values within either interval cannot be classified from the record.

The crossover structure could affect precision if within-person correlations are incorporated. Since paired differences and the sponsor model details are not reported, the available summaries do not allow a full assessment of that contribution. The intervals describe uncertainty for their respective analyses, not certainty about whether the two conditions are equivalent.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total event counts. The registry's planning illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers effects set at the stated fraction of the observed effect. The planning assumptions are an illustration based on the observed effect, not the original trial's design assumptions; the trial's own sample-size justification is not reported in the registry record.

In plain language, the 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions, if that effect and model were correct. The 90% power column gives the corresponding planning figure for a higher chance of detection. These are design calculations, not guarantees about the outcome of a future study.

The rows consider planning for 100%, 75%, and 50% of the observed effect. As the effect to be detected becomes smaller, the illustration requires more participants per arm. For example, the primary-endpoint planning figures range from 847 participants per arm for 80% power at 100% of the observed effect to 3,385 participants per arm for 80% power at 50% of the observed effect. The corresponding 90% figures are 1,133 and 4,531 participants per arm.

These figures are not observed power. They do not describe the probability that the completed study detected its effect, and they should not be mistaken for the actual trial enrollment or the number analyzed. The illustration uses simplified assumptions and does not reflect unreported design details such as the crossover structure or paired-data correlation.

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 = -2.300; pooled standard deviation σ = 16.886.
2. n = 2 × (1.96 + 0.842)² × 16.886² / -2.300² = 846.1, rounded up to 847 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 <- -2.30000000000001                      # observed difference in means
sigma <- 16.8857928448741                     # 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(5528770)
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 = 847 (80% power), 1,133 (90% power)
 75% of observed effect: n per arm = 1,505 (80% power), 2,014 (90% power)
 50% of observed effect: n per arm = 3,385 (80% power), 4,531 (90% power)
power.t.test: 847.1 
Simulated power at n = 847 per arm: 0.797 (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 the sponsor's own primary analysis as a two-sided t-test of final values, with a mean difference of 2.23, a 95% confidence interval from -3.8 to 8.3, and p = 0.429. This is the analysis reported by the trial record. The interval includes zero, and the result does not establish a difference between conditions.

The separate recalculation uses the posted means and standard deviations and gives an unadjusted mean difference of -2.3 for without BPS relative to with BPS, with a 95% confidence interval from -16.41 to 11.81 and p = 0.749. It is a simple reconstruction from summary statistics, not a reproduction of the sponsor's test. In particular, the registry does not report the paired measurements, analysis model, or contrast convention needed to reconcile the estimates and their directions.

The two results should therefore be read according to their stated roles. The sponsor result is the trial's reported analysis; the recalculation is an independent unadjusted summary-based calculation that can provide a check on scale and uncertainty but cannot replace the analysis that used the trial's own data and methods. The registry does not provide enough methodological detail to explain the difference between them.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists three secondary outcomes. Whether the statistical analysis controlled the overall chance of false-positive findings across multiple outcomes is not reported in the registry record. A multiplicity strategy might prioritize a single primary outcome, adjust significance thresholds, or define a testing sequence; no such strategy is stated. Consequently, secondary results should be interpreted cautiously, and their unadjusted p-values, where reported, should not be treated as confirmatory evidence without further analysis-plan information.

The analysis population is not reported in the registry record. Enrollment is recorded as 15, while each primary outcome condition summary reports 11 observations. The record does not explain the relationship between these figures, identify exclusions, or state whether all randomized participants were included in the analysis. It also does not report whether the analysis followed an intention-to-treat, per-protocol, or another population definition.

Missing data handling is not reported in the registry record. The registry entries do not say whether any CGM measurements or participant-period observations were incomplete, how incomplete monitoring was treated, or whether any imputation was used. For a percentage based on CGM values, the completeness and processing of the recorded series can affect the endpoint, but the registry does not provide the details needed to assess that issue.

The crossover structure raises additional analysis questions. The registry describes two treatment sequences, but does not report the methods used to account for period, sequence, or possible carryover effects, nor how within-person dependence was handled. Interim analyses and the detailed statistical analysis plan are not reported in the registry record. These absences limit independent evaluation of the sponsor's reported test and its relationship to the design.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports no serious adverse events in either condition: 0 of 11 at risk with FCL and BPS, and 0 of 11 at risk with FCL without BPS. It also reports 0 deaths in each condition. For other adverse events, it reports 0 of 11 with BPS and 1 of 11 without BPS.

These counts are descriptive records from the study and should be read in the context of the reported at-risk groups. They do not establish that a condition has no safety risk. In general, an absence of observed serious events in a small study does not rule out uncommon harms, and event counts do not establish that an event was caused by a particular device condition. The registry does not provide further event details or a causal assessment for the one other adverse event.

The safety figures are distinct from the primary glucose outcome and do not resolve the study's broader safety and feasibility question. The registry record does not report additional details that would support a more comprehensive safety assessment.

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

The posted results describe a small randomized crossover comparison of full closed-loop delivery with and without an automated Bolus Priming System. For daytime time in range, the group means are 67.4 with BPS and 65.1 without BPS. The sponsor's reported analysis and the summary-based recalculation both have confidence intervals that include zero, while the recalculated interval is broad. These findings leave substantial uncertainty about the size and direction of a difference.

They do not establish that the conditions are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the effect lies within that margin; neither is reported in the registry record. Nor do the results demonstrate that one condition is superior. The p-values do not measure the probability that either treatment is effective, and statistical compatibility with no difference is not proof that no difference exists.

The primary outcome captures daytime CGM time in a specified range, rather than all aspects of glucose control, post-meal response, safety, or device feasibility. The listed secondary outcomes broaden the intended assessment, but detailed results for all of them are not reported in the registry record. The adverse-event counts provide limited descriptive information and cannot rule out less common events.

In general, interpretation should consider the endpoint, design, uncertainty, and analysis methods together. Here, key details about crossover analysis, missing data, multiplicity, and the analysis population are not reported. The record therefore supports a restrained account of the posted comparisons, not a broad conclusion about clinical benefit or device performance.

18. Why This Trial Matters Statistically

This study raises an important statistical issue for automated insulin delivery research: a device feature intended to act around meals may be evaluated using glucose summaries that aggregate measurements across a longer daytime period. Such a summary is useful for describing time in a target range, but it may not isolate the specific postprandial response that motivates the feature. Endpoint choice should match the scientific question, and the registry's primary measure is a broad daytime summary.

The crossover design is also statistically consequential. When the same participants experience both conditions, within-person comparisons can help separate treatment-condition differences from stable variation between people. That benefit depends on appropriate paired analysis and clear reporting of sequence, period, and missing-data handling. The registry describes the sequence structure, but does not report enough analysis detail to establish how those design features were addressed.

The comparison illustrates why estimates and confidence intervals matter alongside p-values. The posted point estimates are near one another, yet the intervals leave room for effects in both directions. A non-significant result is not an equivalence finding, and the imprecision means that a potentially relevant difference cannot be ruled out solely from these summaries.

Finally, the distinction between the sponsor's analysis and an unadjusted recalculation is a useful reporting lesson. Summary statistics enable a transparent approximate check, but they cannot reproduce a design-aware analysis when paired data and model details are absent. Clear reporting of the analysis population, crossover model, uncertainty, and all registered outcomes would make the evidence easier to interpret.

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.

Several limitations specific to this record constrain interpretation. The registry lists enrollment as 15, while the primary outcome summaries report 11 observations for each condition. The record does not explain this difference or define the analysis population. It is therefore not possible to determine from the posted information how many participants contributed complete paired outcome data or why observations may be absent.

The crossover design is described as two treatment sequences with separate 24-hour periods, but the text describing the interval between periods is truncated. The registry does not state how period or sequence effects, carryover, or within-person correlation were handled. These omissions matter because a crossover comparison depends on the relationship between a participant's measurements under the two conditions.

The primary endpoint summarizes daytime time in range rather than an isolated postprandial response. The registry's stated purpose includes safety and feasibility, but the posted outcome details do not give a detailed feasibility result. Detailed results for two listed secondary outcomes are also not reported in the registry record. The safety counts are limited and do not provide detailed event descriptions or causal assessments.

The sponsor's reported test and the unadjusted recalculation yield different point estimates and contrast directions, and the registry does not explain their relationship. The analysis plan, missing-data procedures, multiplicity strategy, original sample-size assumptions, and full model specification are not reported. These gaps make it difficult to reproduce or fully evaluate the primary analysis from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of The Postprandial Impact of Automated Priming Bolus for Full Closed Loop Insulin Delivery — NCT05528770.
• Registry record last updated 2025-09-08; status last verified 2025-08.
• Results first posted 2024-07-09.
• 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

NCT05528770 is a completed randomized, unmasked crossover study of full closed-loop insulin delivery with and without a Bolus Priming System in people with type 1 diabetes. The registry lists enrollment of 15 and records the study dates as 2022-10-20 to 2023-01-13. The primary endpoint is daytime percentage of CGM values between 70 and 180 mg/dL over 18 hours.

The sponsor reports a two-sided t-test of final values, while a separate unadjusted recalculation from group summaries gives a different estimate and confidence interval. Both reported intervals include zero, and the recalculation is imprecise. The registry does not provide enough analysis detail to reconcile the estimates or assess all crossover features. Safety summaries report no serious adverse events or deaths in either condition and one other adverse event without BPS.