The International Diabetes Closed Loop (iDCL) Trial: Protocol 4: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The International Diabetes Closed Loop (iDCL) Trial: Protocol 4 (NCT04436796), a randomized na study. The primary outcome is Percent CGM Time in Range 70-180 mg/dL.

2. Clinical Question

3. Trial Design

This was a randomized crossover comparison in an outpatient setting. In a crossover design, participants receive or use each intervention condition in sequence, so the intended comparison can use measurements from the same participants under both conditions. That design can help control for stable differences between people. The registry record identifies the trial as randomized and crossover, but does not report the intervention sequence, period-specific results, washout arrangements, or the statistical method used to account for the crossover structure.

The artificial pancreas condition used the iAPS system, described as a phone platform with a study insulin pump, study CGM, and study glucometer. The comparator condition used a participant’s home insulin pump with a study CGM and glucometer. Participants could use PLGS mode on the home pump if the feature was supported and compatible with the study sensor. The comparator therefore represents SAP use with possible PLGS rather than a uniformly specified PLGS setting.

The registry reports 35 enrolled participants and 35 observations in each intervention condition for the primary outcome. Because this is a crossover trial, those arm-level sample sizes should not be interpreted as separate groups of 35 people. The record does not report the number contributing paired measurements or the analysis population definition. The study status is completed, and the registry dates are 2020-08-05 for study start and 2021-05-10 for primary completion. Masking was listed as none. The record does not report further details about adherence, treatment-period duration, or reasons for any missing measurements.

The primary outcome was mean percent CGM time in the 70-180 mg/dL range over 13 weeks. The posted results also include selected CGM measures of average glucose, time above specified thresholds, and other secondary outcomes. A detailed protocol, a statistical analysis plan, and the original sample-size rationale are not reported in the registry record. Thus, the posted summaries describe the outcomes, but they do not establish how the investigators prespecified every analysis or handled the crossover design in their original 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.

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 Percent CGM Time in Range 70-180 mg/dL, measured over 13 weeks.

The primary endpoint was the mean percentage of CGM time spent between 70 and 180 mg/dL over 13 weeks. It describes the share of monitored time that falls within the stated glucose range, rather than a single glucose reading or a count of clinical events. A higher mean percentage indicates that a greater share of monitored time was within that range in the observed data.

Time in range is used as a continuous measure of glucose exposure: it reflects both how often glucose readings fall within the specified interval and how long they remain there. CGM measurements can capture variation across daily life that isolated measurements may not represent. The endpoint is therefore relevant to comparing glucose patterns under the two device conditions. It does not, by itself, measure every aspect of diabetes management or establish effects on longer-term clinical outcomes.

The registry reports a mean of 69.0% for the artificial pancreas condition and 66.0% for SAP/PLGS, each with a standard deviation of 14.0. The posted outcome description identifies the measure as mean percent time in range. The registry record does not report further information about how CGM gaps, invalid readings, or participant-level summaries were handled. Those details matter because the calculation depends on which monitoring data are included and how the recorded time is aggregated.

7. Results Posted in the Registry

• Sensor Augmented Pump/Predictive Low Glucose Suspend: mean 66.00 versus 69.00 on control; difference -3.00 (95% CI -9.56 to 3.56), standardized effect d = -0.21; z-test p = 0.370.

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 Mean Glucose

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Sensor Augmented Pump/Predictive Low Glucose Suspend: mean 156.00 versus 158.00 on control; difference -2.00 (95% CI -13.54 to 9.54), standardized effect d = -0.08; z-test p = 0.734.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sensor Augmented Pump/Predictive Low Glucose Suspend and the control. The interval gives the range of effects that remain compatible with the data.

CGM Time > 180

• 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:
  • Sensor Augmented Pump/Predictive Low Glucose Suspend: mean 30.00 versus 29.00 on control; difference 1.00 (95% CI -6.27 to 8.27), standardized effect d = 0.06; z-test p = 0.787.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sensor Augmented Pump/Predictive Low Glucose Suspend and the control. The interval gives the range of effects that remain compatible with the data.

CGM Time > 250

• 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:
  • Sensor Augmented Pump/Predictive Low Glucose Suspend: mean 8.00 versus 9.00 on control; difference -1.00 (95% CI -4.75 to 2.75), standardized effect d = -0.12; z-test p = 0.601.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sensor Augmented Pump/Predictive Low Glucose Suspend and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover complementary aspects of CGM patterns, including average glucose, time above specified thresholds, time below thresholds, time in a narrower range, coefficient of variation, and standard deviation. The registry lists 22 secondary outcomes, while the posted numerical summaries include selected measures. Together, these outcomes describe related features of glucose exposure and variability rather than independent questions wholly separate from the primary endpoint.

The available secondary summaries do not suggest a strong, consistent separation between the device conditions across the reported measures. Their unadjusted mean differences are small relative to the uncertainty intervals, and the intervals include zero. This broad pattern is directionally compatible with the primary result’s uncertainty: the summaries do not establish a clear condition difference in the measures with posted comparisons. Individual secondary results should not be treated as confirmation or contradiction of the primary result in isolation.

Secondary outcomes are often useful for describing whether a primary-outcome pattern is accompanied by changes in related measures. However, many outcomes create many opportunities for apparently notable findings to arise by chance. Unless a multiplicity strategy is specified, unadjusted p-values from secondary outcomes carry less weight than a prespecified primary analysis. The registry record does not report a multiplicity adjustment or a hierarchy for testing secondary outcomes. It also reports no analyses for the listed secondary outcomes.

These data should therefore be read as descriptive context, not as a collection of independent confirmatory tests. The endpoints are correlated because they are derived from related CGM records, and the registry does not report how their tests were planned or adjusted. The overall pattern can help characterize the posted outcomes, but it does not support expanding the primary conclusion into a claim about every measure of glucose exposure, variability, or safety.

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

• CGM Mean Glucose
• CGM Time > 180
• CGM Time > 250
• CGM Time < 70
• CGM Time < 54 (Superiority)
• Coefficient of Variation
• CGM Time in Range 70-140 mg/dL
• Standard Deviation

9. Statistical Interpretation

10. Statistical Methods Explained

The results describe a continuous outcome, summarized by means and standard deviations. A mean is the arithmetic average of the measured values. A standard deviation describes how dispersed those observations are around their mean. For the primary endpoint, the mean is the average percentage of CGM time in the 70-180 mg/dL range, while the standard deviation of 14.0 describes variability in the outcome values across observations. These summaries answer different questions: the mean describes the central level, and the standard deviation describes spread.

What does the mean difference represent?

The posted primary contrast is a mean difference of -3.0. Its direction is consistent with expressing SAP/PLGS relative to the artificial pancreas: the SAP/PLGS mean was 66.0%, compared with 69.0% for the artificial pancreas. Since the endpoint is measured as a percentage of time, the contrast is interpreted in percentage points. It is not a relative percentage change. No additional conversion is needed to understand the reported contrast.

A contrast is useful because it places the group summaries on a common scale. But the contrast does not explain why the outcomes differ or whether an observed difference is important in practice. Interpretation also depends on uncertainty, design, outcome measurement, and the analysis population. The record does not report a prespecified threshold for a meaningful difference in time in range.

What do the confidence interval and p-value say?

A confidence interval communicates uncertainty around an estimated contrast. In general, a wider interval indicates less precision, while a narrower interval indicates greater precision. The primary 95% confidence interval extends from -9.559 to 3.559. Because the interval includes zero, the data do not establish a nonzero contrast under this unadjusted calculation. The interval also makes clear that the estimates are not precise enough to identify a single direction or magnitude with confidence.

The p-value of 0.37 is an unadjusted result. In general, a p-value measures how incompatible observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The registry record does not report the model or test used for the trial’s original analysis. The posted p-value and interval should therefore be understood as unadjusted recalculations from summary statistics.

Why does the crossover design matter?

In a crossover trial, the same participant may contribute measurements under both conditions. This often allows a within-participant comparison, which can account for stable characteristics shared across periods. The statistical analysis may need to consider the pairing, treatment period, sequence, and possible carryover. The registry record identifies the design as crossover but does not report those analysis details, the individual paired data, or period-level outcome summaries. The simple unadjusted recalculation from arm summaries does not recover the information in paired observations and should not be mistaken for a crossover-adjusted trial analysis.

The record lists 35 observations in each condition and an enrollment of 35. That presentation is consistent with arm summaries for a crossover trial, but it does not disclose whether every enrolled participant contributed complete measurements to both conditions. The number of complete pairs and the handling of incomplete records are not reported in the registry record. Without participant-level data and analysis details, the posted summaries cannot establish how within-person correlation affected uncertainty.

What does the standard deviation contribute?

Standard deviations help describe outcome variability but do not directly quantify uncertainty in the difference between condition means. In general, uncertainty in a contrast depends on the variability, sample size, and the relationship between observations. In a crossover setting, the relationship between a participant’s measurements under the two conditions can be important. Since the registry does not report paired variability, the recalculated uncertainty cannot incorporate that relationship. The reported standard deviations remain useful descriptive information, but they are not a substitute for the trial’s full analysis.

The arm-level standard deviations for the primary outcome were both 14.0. The posted summaries thus show similar marginal spread in the two conditions. Similar standard deviations do not imply that individual participants had similar results under both conditions, because the paired association is not described. No assumption about that association should be inferred from the arm summaries alone.

What can be concluded from the reported analyses?

The registry reports no analyses for the primary outcome and no reported analyses for the listed secondary outcomes. The contrasts and p-values described in the results are simple unadjusted recalculations from posted summary statistics. They are useful for describing the magnitude and uncertainty visible in those summaries, but they do not replace the sponsor’s analysis if a sponsor analysis is reported elsewhere. The registry record does not report a detailed statistical analysis plan, multiplicity procedure, missing-data method, or analysis-population definition.

General statistical practice distinguishes descriptive summaries from prespecified inferential analyses. A prespecified analysis can define the outcome, population, model, handling of repeated measurements, and decision criteria before outcomes are examined. The registry record does not provide those details, so it is not possible to judge whether a particular model or adjustment was part of the original plan. The observed summary values should not be used to infer protocol decisions that are not documented.

11. Confidence Intervals and Precision

The primary mean difference was -3.0 percentage points, with a 95% confidence interval from -9.559 to 3.559. This interval is wide enough to include zero and estimates on either side of zero. It therefore leaves uncertainty about both the direction and size of the contrast. The interval is more informative about precision than the point estimate alone: the point estimate is one summary of the observed contrast, while the interval describes a range of values compatible with the unadjusted recalculation.

The interval should not be interpreted as a range containing a fixed proportion of individual participants’ outcomes. It concerns uncertainty in the estimated mean difference, not the distribution of individual time-in-range values. The standard deviation of 14.0 in each condition describes variation in the outcome observations, while the confidence interval describes uncertainty around the contrast. These are distinct quantities and answer different questions.

Because the study used a crossover design, precision may depend on within-participant association as well as marginal variability. The registry record does not report the paired data, paired standard deviation, or the method used in the original crossover analysis. The interval is an unadjusted recalculation from posted summary statistics and may not capture every design feature that a trial-specific analysis would use.

The unadjusted p-value was 0.37. This is consistent with the confidence interval including zero, but it should not be treated as evidence that the conditions are equivalent. The interval shows that a range of contrasts remains compatible with the summary statistics. The record does not report a prespecified equivalence margin or an analysis intended to establish equivalence. Accordingly, the precision supports a cautious description of the observed estimates rather than a definitive claim about the absence of a difference.

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 original trial’s design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at 100%, 75%, or 50% of the observed effect. For these continuous-outcome comparisons, the figures are participants per arm, not total events. The planning assumptions for the trial’s original design are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is the true effect and the model assumptions apply. The 90% power column gives the corresponding planning estimate for a 90% chance. These are prospective planning quantities, not probabilities that the current trial’s result is correct. This is not observed power.

The estimates depend strongly on the assumed effect size. Planning for 100% of the observed effect gives 342 participants per arm for 80% power and 458 for 90% power. Planning for 75% of the observed effect gives 608 and 814 participants per arm, respectively. Planning for 50% of the observed effect gives 1,368 and 1,831 participants per arm. The pattern illustrates a general principle: smaller effects are harder to distinguish from random variation, so detecting them with the same power generally requires more participants.

These figures are not recommendations and do not show what enrollment would have been appropriate for the trial. They are calculated from the observed effect, which is uncertain and may not represent the effect a future study should target. The registry does not report the study’s original sample-size justification, its assumed effect, or its planned power calculation. The planning values should therefore be read as illustrations of how sample size changes under the stated assumptions, not as evidence about the trial’s design quality or the reliability of its observed 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 = -3.000; pooled standard deviation σ = 14.000.
2. n = 2 × (1.96 + 0.842)² × 14.000² / -3.000² = 341.9, rounded up to 342 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 <- -3                      # observed difference in means
sigma <- 14                     # 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(4436796)
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 = 342 (80% power), 458 (90% power)
 75% of observed effect: n per arm = 608 (80% power), 814 (90% power)
 50% of observed effect: n per arm = 1,368 (80% power), 1,831 (90% power)
power.t.test: 342.8 
Simulated power at n = 342 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 record does not report a multiplicity plan for the secondary outcomes. Multiplicity arises when investigators examine several outcomes or comparisons: even when each test uses the same nominal threshold, the chance of at least one apparently notable result can increase across a collection of tests. Statistical approaches such as adjusting thresholds, defining an outcome hierarchy, or designating analyses as exploratory can address this issue, but the record does not state that any such approach was used. Unadjusted secondary results should consequently be interpreted cautiously.

The record lists 22 secondary outcomes and reports no analyses for them. Several types of CGM measures appear among the listed outcomes, including time above and below glucose thresholds and measures of variability. These outcomes may be correlated because they draw on the same monitoring data. That relationship further complicates interpretation of separate unadjusted tests: the results are not necessarily independent evidence.

Missing-data procedures and analysis populations are not reported in the registry record. It does not specify how incomplete CGM records, missed visits, or participants without outcome measurements were handled, nor does it define an intention-to-treat, per-protocol, or other analysis population. Enrollment was 35, and the primary arm summaries each report 35 observations, but these figures alone do not describe data completeness across crossover periods or identify how all enrolled participants contributed to the estimates.

The record also does not report the original model, the handling of period and sequence, or whether the analysis accounted for within-participant correlation. These details are important in a randomized crossover trial because participants may contribute measurements under both conditions. Without the original statistical analysis plan and participant-level results, the posted arm-level summaries cannot establish whether those features were handled in the trial’s analysis.

These reporting gaps do not show that a particular method was or was not used; they mean the method is not documented in the registry record. The unadjusted recalculations should be treated as limited summaries rather than as a complete account of the trial’s prespecified inferential 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: severe hypoglycemia (2.9%).

The registry reports serious adverse events among 35 participants at risk in each condition. The artificial pancreas condition had 0 serious adverse events, while the SAP/PLGS condition had 1. The record lists Severe Hypoglycemia as a serious adverse event term at 2.9%. There were 0 deaths in either condition. These are event counts and a listed event term, not a complete description of each event’s timing, duration, or relationship to the device condition.

For other adverse events, the registry reports 4 affected participants in the artificial pancreas condition and 0 in the SAP/PLGS condition, with 35 at risk in each. The record does not provide further event details in the information. The figures should be read as registry counts for the stated groups, not as exposure-adjusted rates. In a crossover trial, the same participant may experience both conditions; the record does not clarify how event attribution or participant overlap was handled.

The counts are small and provide limited information about comparative safety. They do not establish that one condition is safer or less safe. The registry does not report detailed event narratives, event severity beyond the serious-event listing, or an analysis comparing safety between conditions.

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

The primary result describes mean CGM time in range during the 13-week outcome timeframe for the two device conditions. The posted means were 69.0% for the artificial pancreas and 66.0% for SAP/PLGS. The unadjusted contrast was -3.0 percentage points for SAP/PLGS relative to the artificial pancreas, with a 95% confidence interval from -9.559 to 3.559. This is a summary of the observed CGM measure, not a complete assessment of all possible benefits, risks, or outcomes.

The confidence interval includes zero and ranges across estimates in both directions. Thus, the posted summary does not establish a clear difference between conditions. It also does not establish that the conditions are equivalent. A conclusion of equivalence would require a prespecified margin and a suitable analysis, neither of which is reported in the registry record. The result should not be converted into a claim that either device works or does not work.

The trial’s randomized crossover design means participants could contribute experience under both conditions. That design can support a within-participant comparison, but the registry does not report paired results or the original analysis method. The unadjusted recalculation from arm summaries may not reflect the full information or structure of a crossover analysis. Missing-data handling, analysis-population definitions, and the original statistical plan are also not reported.

Secondary CGM measures provide additional descriptive context, but their unadjusted results carry less weight when the record does not report a multiplicity strategy. The safety counts are likewise limited: they describe reported event counts but do not give enough detail to characterize comparative safety comprehensively. The registry record therefore supports a careful description of the posted summaries and their uncertainty, rather than broad conclusions beyond the measured outcomes and reported follow-up.

17. Why This Trial Matters Statistically

This trial is statistically notable because it compares device conditions in a randomized crossover design, where participants may contribute outcome measurements under both conditions. Such designs can make within-person comparisons informative by controlling for stable differences between participants. At the same time, the analysis needs to account for the paired structure and potentially for period and sequence. The registry identifies the crossover design but does not report whether or how those features entered the original analysis.

The contrast between the posted primary means is modest relative to the variability reported for the outcome, and its unadjusted confidence interval is broad enough to include zero and estimates in either direction. This illustrates why a point estimate alone is not an adequate summary of a trial result. Precision and design-specific analysis matter, especially when interpreting a small study with a continuous outcome.

The record also illustrates the distinction between a trial’s observed sample size and a future planning calculation. The planning illustrations are based on fractions of the observed effect and explicit assumptions, while the original sample-size justification is not reported. Those illustrations show how a smaller target effect requires more participants under the stated assumptions; they do not indicate the power of the completed trial.

Finally, the range of secondary CGM outcomes shows why multiplicity and prespecification matter. Related measurements can describe different features of glucose patterns, but multiple unadjusted tests are not equivalent to multiple independent confirmations. Clear reporting of analysis populations, missing-data methods, crossover models, and multiplicity procedures would make the results easier to interpret and reproduce.

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 registry record leaves important trial-specific details unreported. It does not describe the original statistical analysis plan, the sample-size justification, or the model used to account for the randomized crossover design. In particular, it does not provide paired outcome summaries, period-specific results, sequence details, or information about how potential carryover was addressed. The unadjusted recalculated comparison cannot substitute for those design-specific details.

The registry also does not report the analysis population, how missing CGM data were handled, or whether all participants contributed measurements under both conditions. Although enrollment was 35 and each primary condition summary reports 35 observations, those totals do not show completeness at the participant-period level. The record does not describe adherence or how use of PLGS varied among participants in the comparator condition.

Masking was listed as none. The primary endpoint is based on CGM measurements, but the record does not report details about outcome-data processing or whether any outcome assessment procedures were blinded. The comparator could include PLGS depending on home-pump support and sensor compatibility, so comparator use may not have been uniform. This is relevant when interpreting the intervention contrast as a comparison of the conditions as implemented.

The record lists multiple secondary outcomes but does not report a multiplicity procedure, and no analyses are reported for those outcomes. Safety information is limited to group counts and a listed serious-event term; detailed event descriptions and comparative analyses are not reported. These limitations restrict the conclusions to the posted summaries and prevent a full assessment of the trial’s original inferential analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The International Diabetes Closed Loop (iDCL) Trial: Protocol 4 — NCT04436796.
• Registry record last updated 2022-12-02; status last verified 2022-11.
• Results first posted 2022-12-02.
• 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

NCT04436796 is the completed International Diabetes Closed Loop Trial: Protocol 4, a randomized crossover comparison in people with type 1 diabetes. It compared an interoperable artificial pancreas system using adaptive model predictive control with sensor-augmented pump use, which could include predictive low glucose suspend. The primary endpoint was mean CGM time in the 70-180 mg/dL range over 13 weeks.

The posted primary means were 69.0% for the artificial pancreas and 66.0% for SAP/PLGS. The unadjusted mean difference was -3.0 percentage points, with a 95% confidence interval from -9.559 to 3.559 and an unadjusted p-value of 0.37. The interval includes zero and is compatible with estimates in either direction. The registry record does not report the original crossover analysis, the analysis population, missing-data procedures, multiplicity plan, or original sample-size rationale.