The Bihormonal iLet Bionic Pancreas Feasibility Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Bihormonal iLet Bionic Pancreas Feasibility Study (NCT03840278), a randomized phase 2, phase 3 study. The primary outcome is Percentage of Time That Valid CGM Glucose Readings Are Captured by the iLet Bionic Pancreas.

2. Clinical Question

The comparison is a feasibility question about device data capture under home-use conditions. It asks whether the bihormonal configuration and insulin-only configuration differ in the proportion of time that the device receives valid CGM readings. This outcome is relevant to whether the system has usable glucose information available to guide its control algorithm. It should not be confused with time in a glucose target range, average glucose concentration, or the frequency of hypoglycemia; those are separate outcomes in the registry record.

The study also posted secondary measures related to glucose concentration, time within the 70-180 mg/dl range, time with glucose below 54 mg/dl, and carbohydrate use to treat or prevent hypoglycemic events. These measures describe other aspects of device use and glucose experience, but they do not change what the primary endpoint measures. The primary comparison is between the two device configurations, not between the iLet and no device or usual care.

3. Trial Design

The registry lists this as a randomized, non-masked crossover study with phase labels of phase 2 and phase 3. It was sponsored by Massachusetts General Hospital and is marked completed. The study concerned type 1 diabetes mellitus. Its stated objective was to evaluate the bihormonal iLet configuration delivering dasiglucagon in comparison with the insulin-only iLet configuration in a home-use study in adults with type 1 diabetes.

In a crossover design, participants receive the study conditions in an assigned sequence rather than remaining in a single parallel group throughout. The registry describes sequences beginning with the bihormonal configuration and then moving to insulin-only, or beginning with insulin-only and then moving to the bihormonal configuration. This design can make each participant's experience under the alternate configurations informative for the comparison, provided the analysis accounts appropriately for the repeated observations and order of exposure. The registry record does not report the statistical model used to account for crossover structure, period effects, or possible carryover.

The trial is listed as randomized and non-masked. The registry lists enrollment of 12, while the posted primary outcome gives n=10 for each configuration. It does not report how these outcome counts relate to enrollment, why any outcome data may be absent, or whether all randomized participants contributed to every measure. The arm descriptions state that each sequence used the iLet Bionic Pancreas and a Dexcom G5 Continuous Glucose Monitor, with the pump's control algorithm dosing insulin and/or dasiglucagon based on glucose readings.

The study started on 2019-05-15, and primary completion is listed as 2019-07-03. It is a feasibility study with a small posted outcome sample. Its results therefore describe the reported experience in this study; they do not establish how the configurations would compare in a larger or different population. The original design rationale, target sample size, planned analytic model, and rationale for the phase labels are not reported in the registry 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: 2 were ineligible due to lacking a designated contact or were taking arrhythmogenic medications

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 Percentage of Time That Valid CGM Glucose Readings Are Captured by the iLet Bionic Pancreas, measured over Days 1-7.

The primary endpoint is the percentage of time that valid CGM glucose readings are captured by the iLet Bionic Pancreas during Days 1-7. In practical terms, it summarizes how much of the specified observation period contained usable glucose readings available to the device. The registry description gives a goal of at least 80% for this measure.

This is a continuous endpoint reported as a mean and standard deviation. A mean describes the average percentage of time across the participants represented in each configuration's posted results. The standard deviation describes how much individual values vary around that mean; it is not a confidence interval for the mean and does not itself show the precision of the between-configuration comparison.

Valid data capture is relevant to device operation because the algorithm is described as using CGM glucose values. A greater proportion of time with valid readings would indicate more complete availability of those inputs over the measured period. However, data capture is not itself a direct measure of glucose concentration, time in range, safety, or health benefit. Those are distinct questions, and the registry lists several glucose-related secondary measures separately.

The endpoint is useful for assessing technical feasibility in the study's home-use setting. Its interpretation depends on the measurement window and on what qualified as a valid reading, details beyond the stated endpoint description that are not reported in the registry record. The posted means are close to the stated 80% goal, but the goal is descriptive context, not a reported hypothesis test or a substitute for the comparison between configurations.

7. Results Posted in the Registry

• Insulin-Only iLet Bionic Pancreas: mean 91.00 versus 89.20 on control; difference 1.80 (95% CI -3.81 to 7.41), standardized effect d = 0.28; z-test p = 0.529.

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.

Mean Continuous Glucose Monitor Glucose Concentration

• 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:
  • Insulin-Only iLet Bionic Pancreas: mean 149.00 versus 139.00 on control; difference 10.00 (95% CI -0.55 to 20.55), standardized effect d = 0.83; z-test p = 0.063.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Insulin-Only iLet Bionic Pancreas and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Time Across Days 2-7 Within the CGM Glucose Range of 70-180 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:
  • Insulin-Only iLet Bionic Pancreas: mean 71.00 versus 79.00 on control; difference -8.00 (95% CI -15.46 to -0.54), standardized effect d = -0.94; z-test p = 0.036.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Insulin-Only iLet Bionic Pancreas than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Grams of Carbohydrate Per Day to Treat or Prevent Hypoglycemic Events (Reported Daily by Subjects)

• 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:
  • Insulin-Only iLet Bionic Pancreas: mean 16.00 versus 18.00 on control; difference -2.00 (95% CI -17.31 to 13.31), standardized effect d = -0.11; z-test p = 0.798.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Insulin-Only iLet Bionic Pancreas and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address different aspects of glucose experience and device use, so their estimates need not all move in the same direction. The posted summaries show a mixed pattern across mean glucose concentration, time in the 70-180 mg/dl range, and reported carbohydrate use. This variety means the secondary findings do not form a uniformly consistent signal that simply reinforces the primary data-capture comparison. A measure of valid CGM capture concerns availability of readings; the secondary measures concern glucose levels, time in a specified range, and reported responses to hypoglycemic events.

The secondary results are related to the primary question because glucose readings and glucose outcomes are part of the broader performance context for the iLet configurations. They are not interchangeable endpoints. A difference in time in range would not establish a difference in data capture, and data capture alone would not establish a difference in glucose control. The primary result and secondary results should therefore be interpreted as separate pieces of information about feasibility and measured outcomes.

Unadjusted secondary results carry less weight for confirmatory claims because the registry lists multiple outcomes and does not report a multiplicity procedure or testing hierarchy. When several comparisons are examined, a nominally small p-value can arise by chance even if there is no underlying difference. This general concern does not invalidate an observed estimate, but it makes an isolated unadjusted finding less conclusive. The registry also does not report a prespecified analysis plan or a trial analysis listing that would show which secondary comparisons were planned as confirmatory.

The appropriate overall reading is descriptive and cautious: the secondary estimates add context, but their varied directions and unadjusted status do not establish a coherent, definitive treatment effect. Confidence intervals, outcome meaning, and the small posted outcome sample matter alongside p-values. The registry record does not report enough about analysis populations, missing data, or multiplicity to support stronger claims about how these outcomes should be ranked.

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

• Proportion of Time With CGM Glucose < 54 mg/dl
• Mean Continuous Glucose Monitor Glucose Concentration
• Proportion of Time Across Days 2-7 Within the CGM Glucose Range of 70-180 mg/dl
• Mean Grams of Carbohydrate Per Day to Treat or Prevent Hypoglycemic Events (Reported Daily by Subjects)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted continuous outcomes are presented as means with standard deviations. A mean is the arithmetic average of the observed values represented in a group. A standard deviation describes the spread of those values around the mean. It is not a measure of uncertainty in the mean difference, and a larger standard deviation does not automatically mean that a treatment comparison is less precise: precision also depends on the number of observations and the structure of the design.

What does the mean difference represent?

For each posted comparison, the contrast is oriented as the insulin-only configuration relative to the bihormonal configuration. The mean difference is the insulin-only mean minus the bihormonal mean. A positive estimate means the posted mean is higher under insulin-only for that particular outcome; a negative estimate means it is lower. The direction that is favorable depends on the outcome. For example, a higher percentage of time with valid readings has a different interpretation from a higher glucose concentration. Direction alone does not establish benefit.

The posted comparison results include a confidence interval and an unadjusted p-value. The confidence interval gives a range of values compatible with the observed data under the statistical assumptions used to calculate it. The p-value is a measure of how incompatible the data are with a null hypothesis of no difference, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. These are general explanations of statistical concepts; the registry record does not report a detailed account of the test used for each result.

Why does the crossover design matter?

In a crossover study, the same participant can contribute observations under more than one condition. Outcomes within a participant may therefore be correlated. An analysis that accounts for that pairing can use the design differently from an analysis that treats each condition's observations as unrelated. Period and sequence can also matter if outcomes change over time or if earlier exposure affects later measurements. The registry record identifies the study as crossover and lists randomized sequences, but it does not report an analysis model or say how pairing, period, sequence, or carryover were handled. The recalculated contrasts are simple unadjusted re-calculations from posted summary statistics; they should not be mistaken for a reported crossover-model estimate.

The trial's own analysis results are not listed in the registry's analyses section. There is no sponsor analysis result to take precedence over the recalculated comparisons, and the discrepancy flag is false. This does not resolve the missing methodological details: the original analytic plan and the trial's own analysis procedures are not reported in the registry record. Accordingly, the summary comparisons can be described, but the record does not support claims about adjustment or model specification beyond what is explicitly stated.

What does the standard deviation tell the reader?

Standard deviations describe participant-level variability in the posted group values. For the primary outcome, both configurations have the same reported standard deviation, 6.4. That equality describes the displayed spread; it does not mean the observations were paired or that the difference estimate has no uncertainty. For the secondary outcomes, the standard deviations vary by configuration and measure. Wide variation can make an average less representative of each individual result, particularly in a small sample.

In general, over-dispersion is a concern when observed variability is greater than the statistical model expects. If a model assumes less variability than is present, its standard errors and confidence intervals may be too optimistic. The posted outcomes are continuous means with standard deviations, and the registry record does not describe a model for over-dispersion or report diagnostics. It would therefore be inappropriate to assert that over-dispersion was assessed or present. More generally, the adequacy of any model depends on the data structure and assumptions, and those details are not reported in the registry record.

How should p-values be read across outcomes?

The comparison p-values are unadjusted. Each addresses its own contrast without an indicated correction for examining multiple outcomes. When many outcomes are tested, the chance of seeing at least one small p-value by chance can increase. This is a general property of multiple testing, not evidence that any particular result is false. The record lists multiple outcome measures but does not report a multiplicity plan, an outcome hierarchy, or adjusted p-values. A secondary p-value should therefore be viewed as exploratory unless the registry record reports a plan that gives it confirmatory status.

Statistical significance is not the same as practical importance. A p-value alone does not convey the size or precision of the difference, and an interval should be considered alongside the estimate. Conversely, a p-value above a conventional threshold does not prove that there is no effect. In a small feasibility study, estimates can remain uncertain even when the point estimate is close to zero.

What information is missing from the analysis record?

The registry record does not report the prespecified statistical analysis plan, the treatment of missing data, the analysis population, or a crossover-specific model. It also does not describe any interim analyses or sample-size justification. These details are important for understanding whether the posted outcome counts match the intended analysis population, whether all randomized participants were included, and whether the statistical methods followed the original plan. In their absence, interpretation should stay close to the posted means, standard deviations, confidence intervals, and unadjusted p-values, without assuming methods that are not documented.

11. Confidence Intervals and Precision

A confidence interval communicates uncertainty in an estimated difference. For the primary comparison, the estimated mean difference is 1.8 percentage points, and the 95% confidence interval extends from -3.81 to 7.41. The interval includes zero, which is compatible with no mean difference, while also allowing differences in either direction. Thus, the point estimate is not precise enough to rule out a range of potentially different values under the calculation's assumptions.

The confidence interval is more informative about precision than the p-value alone. The unadjusted p-value is 0.529, but it should not be read as the probability that the configurations are the same. Rather, the estimate and interval show that the data do not sharply distinguish a small difference from a larger difference in either direction. The interval is not a prediction interval for an individual participant and does not describe the full range of individual readings.

The group standard deviations, both 6.4 for the primary endpoint, describe variability among the posted observations. The interval for the contrast reflects uncertainty about the difference in means and depends on the analysis assumptions. Because the trial is a crossover study, the handling of within-participant pairing could affect precision. That analysis detail is not reported in the registry record, so the interval should be interpreted as the posted summary-statistic comparison rather than as evidence that a specific crossover model was used.

Precision is limited by the small outcome counts, with n=10 reported for each configuration, and by the absence of a reported analysis plan or missing-data account. The registry record does not state an equivalence margin or a precision target. The interval therefore cannot be used to conclude that the two configurations are equivalent, nor does it establish that the observed estimate is clinically important. It describes the uncertainty around the posted comparison under its calculation assumptions.

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 effects, not the trial's original design assumptions. For these continuous outcomes, the figures are participants per arm, not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the selected effect under those assumptions, if that effect were real and the assumptions held. The 90% power column uses a higher probability of detecting the selected effect, and therefore gives a larger planning count for the same effect fraction. These are hypothetical planning calculations; this is not observed power.

Rows that plan for 100%, 75%, or 50% of the observed effect explore different effect sizes. Smaller effects are harder to distinguish from random variation and require more participants per arm to achieve the same target power. The calculations use the observed effect as their starting point, so they should not be read as independent evidence that the observed effect is reproducible or that it is the effect a future study should expect.

The original sample-size justification, target power, and assumptions used when designing this feasibility study are not reported in the registry record. The posted planning values do not establish that the trial was designed to detect the observed differences, and they cannot turn an inconclusive result into evidence of no effect. The curve should be read in the same planning context as the displayed figures: it illustrates how planning requirements change with the effect size under the stated assumptions, not how much power the completed trial actually had.

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 = 1.800; pooled standard deviation σ = 6.400.
2. n = 2 × (1.96 + 0.842)² × 6.400² / 1.800² = 198.5, rounded up to 199 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 <- 1.8                      # observed difference in means
sigma <- 6.4                     # 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(3840278)
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 = 199 (80% power), 266 (90% power)
 75% of observed effect: n per arm = 353 (80% power), 473 (90% power)
 50% of observed effect: n per arm = 794 (80% power), 1,063 (90% power)
power.t.test: 199.4 
Simulated power at n = 199 per arm: 0.807 (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 multiple outcome measures, including a primary endpoint and secondary measures. The posted secondary comparisons use unadjusted p-values. The registry record does not report a multiplicity adjustment, a hierarchical testing plan, or a prespecified rule for treating any secondary endpoint as confirmatory. Without such information, nominal p-values across the set should not be interpreted as if each were the only test conducted. Examining several outcomes can increase the chance of at least one apparently unusual result even when no true difference exists; this is a general statistical concern.

Missing-data handling is also not reported in the registry record. The primary outcome lists n=10 for each configuration, while overall enrollment is listed as 12. The record does not explain why the counts differ, whether some measurements were missing, or how any missing observations were handled. It also does not state whether the outcome counts represent all randomized participants, participants who completed both periods, or another analysis population. No assumption about the reason for the counts or the missing-data method can be made from the posted information.

For a crossover study, it is important to know how observations from the same participant were related in the analysis and whether period or sequence was considered. The registry identifies randomized sequences, but does not report a model or analysis plan addressing these factors. It also does not report interim analyses, so no claim about whether interim looks occurred is warranted. The record does not report the original sample-size justification or a prespecified analysis population.

These omissions limit the ability to assess whether the posted estimates follow the intended analysis, how robust they are to missingness, or how secondary results were selected and interpreted. They do not by themselves show that the results are biased. They mean that the record does not provide enough detail to evaluate these issues beyond identifying them as unresolved reporting gaps.

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 non-serious adverse event terms

The registry's serious adverse event figures show zero participants affected by serious adverse events in the bihormonal iLet group and zero in the insulin-only iLet group. Deaths are also reported as zero in each group. These figures describe what is posted for the study groups; they do not show that serious events are impossible or that risk is absent.

The registry lists 10 participants at risk for serious adverse events in each configuration. The record does not provide serious adverse event terms, and the serious-event terms list is empty. The trial is small, so the absence of a reported serious event in these groups offers limited information about uncommon harms. The registry record does not report further detail on event timing, severity categories beyond serious status, relatedness, or how events were compared statistically.

These are descriptive safety counts, not a formal risk comparison. Because the study used a crossover design, interpretation of event exposure and attribution would also depend on details not reported in the registry record. The figures should be read as the registry's posted serious-event and death counts during the study, not as proof of comparative safety or as advice about treatment decisions.

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

The primary result describes valid CGM reading capture during Days 1-7 under the two iLet configurations. The reported means are both above the goal stated in the registry description, and the estimated difference is modest with a confidence interval that includes zero. The data do not establish a difference in this primary endpoint. At the same time, they do not demonstrate that the configurations are equivalent or that any meaningful difference has been ruled out.

The result is specific to a small home-use feasibility study in adults with type 1 diabetes, as described in the registry record. It concerns the bihormonal and insulin-only configurations of the iLet, not comparisons with other devices or care approaches. The primary outcome reflects data availability rather than direct clinical benefit. Secondary glucose measures add context but are distinct outcomes and have unadjusted comparisons.

The study's crossover design could be useful for comparing configurations within participants, but the registry record does not report the analysis details needed to determine how the posted comparison accounted for that design. Outcome counts are n=10 in each configuration, while enrollment is listed as 12; the record does not explain that difference. The analysis population and missing-data procedures are not reported.

Accordingly, the posted results should be understood as estimates from this feasibility study, with uncertainty and reporting limitations. A non-significant primary comparison is not proof of no effect. A secondary nominal result is not, by itself, proof of a reliable effect. Neither the primary nor secondary data establish efficacy, equivalence, or generalizability beyond the setting and outcomes described in the registry record. No medical recommendation follows from these statistics.

17. Why This Trial Matters Statistically

This study illustrates why feasibility outcomes and clinical outcomes need to be kept distinct. The primary measure asks whether valid CGM readings were captured over the observation period. That is relevant to device function, but it does not itself tell readers whether glucose levels improved or whether participants experienced fewer clinically important events. The registry's separate secondary measures make those distinctions visible.

It also illustrates the importance of matching interpretation to design. A crossover study can offer within-participant comparisons, but the statistical analysis needs to reflect that structure. The registry identifies randomization and treatment sequences, yet does not report the analysis model, handling of period or sequence, or the analysis population. Without that information, readers should not assume that the displayed group contrast is a fully adjusted crossover estimate.

The primary estimate is accompanied by a confidence interval that permits differences in either direction. This is a reminder that a point estimate and a p-value alone do not settle the question. The small posted outcome counts leave substantial uncertainty, and the absence of a reported equivalence margin means a result that does not establish difference cannot be reinterpreted as proof of sameness.

Finally, the secondary results highlight the interpretive challenge of multiple outcomes. Different measures can tell different parts of the story, and unadjusted secondary tests deserve cautious treatment when no multiplicity plan is reported. The study is statistically instructive not because it settles every comparison, but because it shows why endpoint definitions, design-aware analysis, precision, and transparent reporting all matter in evaluating a clinical trial.

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.

The primary limitation for interpretation is the small outcome sample: n=10 is reported for each configuration. The registry lists enrollment of 12 but does not explain how enrollment relates to the posted outcome counts. The absence of that accounting prevents a clear assessment of whether observations were missing, whether participants completed both sequences, or which analysis population produced the reported summaries.

The crossover design raises questions that cannot be answered from the registry record. It does not report whether the comparison accounted for within-participant correlation, treatment period, sequence, or possible carryover. The posted recalculations are simple unadjusted comparisons of summary statistics, not a substitute for a reported crossover analysis. The registry's analyses listing contains no reported analyses.

The primary outcome is a device data-capture measure, not a direct clinical outcome. The record gives the intended goal and observation window but does not report additional operational detail about criteria for a valid reading. Secondary outcomes broaden the description but introduce multiple comparisons; no multiplicity adjustment or testing hierarchy is reported. The secondary p-values are therefore unadjusted and should be interpreted cautiously.

The trial is listed as non-masked, which can matter for outcomes involving participant reporting, such as daily carbohydrate use. The record does not report procedures intended to limit reporting or measurement bias. It also does not report the original sample-size justification, statistical analysis plan, missing-data methods, or interim-analysis procedures. These limitations constrain interpretation; they do not establish that bias occurred or that the posted results are incorrect.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Bihormonal iLet Bionic Pancreas Feasibility Study — NCT03840278.
• Registry record last updated 2019-12-16; status last verified 2019-11.
• Results first posted 2019-12-16.
• 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 Bihormonal iLet Bionic Pancreas Feasibility Study is a completed, randomized, non-masked crossover study sponsored by Massachusetts General Hospital. The registry lists phase 2 and phase 3 labels, enrollment of 12, and a home-use comparison in adults with type 1 diabetes between the bihormonal iLet configuration and the insulin-only configuration.

The primary endpoint measures the percentage of time valid CGM glucose readings were captured during Days 1-7. Posted means are 89.2% for the bihormonal configuration and 91.0% for insulin-only; the mean difference is 1.8, with a 95% confidence interval from -3.81 to 7.41 and an unadjusted p-value of 0.529. The interval includes zero and does not establish a difference or equivalence.

The registry does not report the crossover analysis model, missing-data methods, analysis population, original sample-size rationale, or multiplicity plan. Secondary findings are therefore best treated as descriptive and exploratory alongside the primary feasibility result.