Evaluation of Fiasp® (Fast Acting Insulin Aspart) in 670G Hybrid Closed-Loop Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Fiasp® (Fast Acting Insulin Aspart) in 670G Hybrid Closed-Loop Therapy (NCT03554486), a randomized phase 4 study. The primary outcome is Percentage of Time in Range: Sensor Glucose Values Between 70-180 mg/dl.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, crossover Phase 4 study of Fiasp and Novolog with the 670G hybrid closed-loop system. In a crossover design, participants receive more than one treatment in sequence, so each participant can contribute observations under both treatment conditions. The registry describes two sequences: Fiasp followed by Novolog, or Novolog followed by Fiasp. It does not report how many participants were assigned to each sequence.

Both sequences began with a 2-week run-in period for pump-setting adjustments and monitoring. Participants then used the first assigned insulin for 2 weeks and the other insulin for 2 weeks. The primary endpoint used sensor-glucose data from 7 days during the second half of each intervention period. The registry says participants and investigators were blinded to which group the participant was assigned to.

The study is described as a pilot outpatient study intended to obtain preliminary data on Fiasp in a closed-loop system and assess whether changes to the 670G pump might need to be made to optimize its use. Enrollment was 27. The primary analysis population is described as participants who completed the protocol; the registry does not report a detailed participant-flow account or explain the difference between enrollment and the 19 observations reported for each treatment in the outcome summaries.

The registry lists Stanford University as sponsor and the study status as completed. Its start date is 2018-07-23 and its primary completion date is 2019-03-30. The original sample-size justification, period or sequence effects, any washout arrangements, and details of the planned crossover analysis 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: 27 participants signed informed consent. 3 participants failed screening and did not enter the run-in period (a 2-week period for pump-setting adjustments and monitoring).

Run-in Period (2 Weeks)

Reasons for not completing this period:

Treatment Period 1 (2 Weeks)

Reasons for not completing this period:

Treatment Period 2 (2 Weeks)

Analysis population for the primary outcome, as defined in the registry: Participants who completed the protocol are included in the analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Participants who completed the protocol are included in the analysis.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Time in Range: Sensor Glucose Values Between 70-180 mg/dl, measured over 7 days (during 2nd half of 2-week intervention period).

The primary endpoint was the percentage of time that sensor glucose values were between 70-180 mg/dl. The reported summary is a mean with a standard deviation, measured over 7 days during the second half of each 2-week intervention period. The outcome therefore describes time in a specified sensor-glucose range, rather than a single glucose reading or a count of clinical events.

In general, a time-in-range measure condenses repeated measurements over a defined observation window into an interpretable summary of how often values fall within a chosen range. It can describe the distribution of sensor readings across that window, while the mean gives a group-level summary and the standard deviation describes variability among the reported observations. This endpoint is useful for comparing glucose patterns under the two insulin conditions, but the registry’s summary does not show each participant’s trajectory, the timing of values outside the range, or how long any such readings lasted.

The results are reported as treatment-period means, but the registry record does not describe how the crossover structure was incorporated into the sponsor’s statistical analysis. It also does not report additional details such as rules for handling missing sensor readings. The endpoint should therefore be read as a defined summary of recorded sensor glucose, with the limits of the posted analysis in mind.

7. Results Posted in the Registry

• Novolog Insulin: mean 75.30 versus 78.40 on control; difference -3.10 (95% CI -9.08 to 2.88), standardized effect d = -0.33; z-test p = 0.309.

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 Sensor Glucose in 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:
  • Novolog Insulin: mean 147.00 versus 146.00 on control; difference 1.00 (95% CI -6.63 to 8.63), standardized effect d = 0.08; z-test p = 0.797.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Novolog Insulin and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome, mean sensor glucose, measured over the same 7-day window during the second half of each intervention period. The secondary comparison offers a related view of the glucose measurements, alongside the primary time-in-range outcome. Read together, the outcome set describes sensor-glucose level and the proportion of time within the specified range, rather than a broad assessment of all clinical outcomes.

The overall pattern should be considered in context: the primary endpoint and the secondary endpoint are distinct summaries of sensor data, and neither can substitute for the other. Their statistical results do not establish a comprehensive treatment effect across outcomes. The registry does not report additional secondary outcomes beyond mean sensor glucose, despite listing three outcome measures and three analyses; the status or details of any other measures are not reported in the registry record.

The registry reports a sponsor analysis for the secondary endpoint and an unadjusted recalculation, but these do not eliminate uncertainty about the analysis structure. As with the primary outcome, the registry does not explain whether the sponsor’s test accounts for the crossover pairing or provide a reconciliation with the recalculation. Each result should be understood as applying to its own endpoint and analysis.

In general, when several outcomes are examined, the likelihood of at least one apparently notable result can increase if each is tested without accounting for the full set of comparisons. Unadjusted secondary results therefore usually carry less confirmatory weight than a prespecified primary analysis, particularly when the number of planned outcomes and multiplicity strategy are unclear. The registry does not report a multiplicity adjustment or a hierarchy of secondary hypotheses. These secondary findings are best treated as supportive or exploratory descriptions, not independent confirmation of the primary result.

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

• Mean Sensor Glucose in mg/dl

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a percentage of time, summarized by a mean and standard deviation. The registry gives a mean for each insulin condition, a recalculated difference, a confidence interval, and two p-values from different analyses. These quantities address related but not identical questions. The mean describes the observed group-level result; the difference summarizes the contrast; the confidence interval describes uncertainty around that recalculated contrast; and a p-value measures how incompatible the data are with a specified null model, under the assumptions of the test.

What does the reported mean describe?

The mean time in range is 78.4% for Fiasp and 75.3% for Novolog. These are treatment-condition summaries over the stated sensor-data window. The standard deviations are 9.3 and 9.5, respectively, and describe variation in the reported observations around their respective means. A standard deviation is not a confidence interval and does not by itself show the precision of the treatment comparison. Nor does a mean reveal whether individual participant results were similar or whether the average reflects a range of different patterns.

How should the recalculated difference be read?

The recalculated contrast is defined as the Novolog mean minus the Fiasp mean, giving -3.1 percentage points. With this ordering, a negative value means the reported mean was lower for Novolog than for Fiasp. The estimate is unadjusted and calculated from posted summary statistics. It does not account for any covariates or crossover-specific features unless those are represented in the underlying summaries, which the registry does not establish.

In general, an unadjusted estimate is a direct comparison without adjustment for other variables. It can be useful as a transparent descriptive contrast, but it may not match a prespecified analysis that accounts for the design or other factors. This study is a crossover trial, where the two treatment observations may be paired within a participant. In general, using that pairing can change the uncertainty of a comparison because repeated observations from one person may be correlated. The registry does not report the participant-level paired data or enough model details to determine how that relationship was handled in the sponsor’s analysis.

What do the p-values tell the reader?

The unadjusted recalculation has p = 0.309. The sponsor’s reported two-sided t-test has p = 0.051. A p-value is not the probability that a treatment has no effect, nor is it a measure of the size or practical importance of a difference. It describes how unusual data at least as inconsistent with the null hypothesis would be under the assumptions of a particular test, if the null hypothesis were true. Interpretation depends on the analysis method and its assumptions.

Because the two p-values come from different reported calculations and the registry does not explain the difference, neither should be silently substituted for the other. The sponsor’s test is the analysis reported by the study; the recalculation is a separate unadjusted comparison based on the posted summaries. The sponsor’s estimate and uncertainty interval are not reported in the registry record, so the p-value alone cannot provide the same information about effect size and precision.

Why does a confidence interval matter?

The recalculated 95% confidence interval extends from -9.078 to 2.878 percentage points for Novolog minus Fiasp. In general, a confidence interval shows the range of values reasonably compatible with the data and the method used, under repeated use of that method. It gives more information than a p-value alone because readers can see both the direction and the spread of plausible contrasts. Here, its inclusion of zero is consistent with the unadjusted p-value not indicating strong evidence against a zero difference under that calculation. It does not establish equivalence or show that important differences are impossible.

What assumptions and design details remain unknown?

The sponsor’s reported method is identified as a two-sided t-test, but the registry does not report whether it was paired, how treatment sequence or period was handled, or whether any adjustment was made. It also does not report the original statistical analysis plan, assumptions about the distribution of the endpoint, or rules for missing sensor observations. In general, t-tests rely on assumptions about the data and the analysis structure; a crossover design makes the choice of independent or paired comparison especially relevant. The available record is not sufficient to verify those assumptions or determine whether the reported test corresponds to a particular model.

The posted recalculation should be understood as a simple unadjusted re-analysis of the summarized treatment results, not as proof that the sponsor’s method was incorrect. The registry does not report a reconciliation of the different p-values. Readers can use the recalculation to understand the scale and precision of the posted summary contrast, while treating the sponsor’s result as a distinct analysis with incompletely described methods.

11. Confidence Intervals and Precision

The recalculated mean difference for Novolog minus Fiasp is -3.1 percentage points, and its 95% confidence interval runs from -9.078 to 2.878. The interval crosses zero, so the recalculation is compatible with a lower mean under Novolog, little or no difference, or a higher mean under Novolog. Its span indicates that the estimate is not highly precise: the data and calculation do not pin down the contrast to a narrow range.

In general, a confidence interval is a range generated by a statistical method to represent uncertainty in an estimate. Its interpretation depends on the method’s assumptions and the analysis structure. The interval is from an unadjusted recalculation using posted summary statistics. It should not be mistaken for a confidence interval from the sponsor’s analysis, which is not reported in the registry record.

The reported group standard deviations, 9.3 for Fiasp and 9.5 for Novolog, describe spread in the outcome, not precision of the contrast itself. Precision also depends on the amount of information and the analysis method. Since the study is a crossover trial, how within-participant pairing is incorporated can matter for uncertainty; the registry does not report enough detail to assess that for the sponsor’s analysis.

The interval does not show that the treatments are equivalent, and it does not rule out every difference that might matter. Equivalence or non-inferiority would require a prespecified margin and a suitable analysis; such a margin and analysis are not reported in the registry record. The sponsor’s p-value of 0.051 also does not supply an estimate interval, so it cannot replace the uncertainty information from the recalculation.

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 for 80% power and participants per arm for 90% power. They are illustrations based on the observed effect, not the trial’s original design assumptions. The stated 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. These are planning calculations, not counts of participants enrolled or analyzed in this crossover study.

In general, power is the probability that a planned study will reject a specified null hypothesis if a particular effect is present and the planning assumptions hold. The 80% power column gives the illustrative number of participants per arm for an 80% chance of detecting the chosen effect under those assumptions. The 90% power column gives the corresponding illustration for a higher chance of detection. Neither column describes the chance that the current result is true, and these figures are not observed power.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the planning estimate changes when the target effect is smaller than the observed estimate. Smaller effects need more participants to detect under otherwise unchanged assumptions. The figures should be read as hypothetical planning scenarios rather than as evidence that a future study would achieve the stated power: actual performance depends on whether the assumptions and analysis match the future study.

The illustrations use an equal-allocation, two-arm framework and do not reflect the registry’s crossover sequence structure or any original sample-size justification. The study’s own design assumptions and sample-size rationale are not reported in the registry record. The figures therefore should not be used to infer why the study enrolled its reported number or how its original investigators planned the analysis.

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 = -3.100; pooled standard deviation σ = 9.401.
2. n = 2 × (1.96 + 0.842)² × 9.401² / -3.100² = 144.4, rounded up to 145 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 <- -3.10000000000001                      # observed difference in means
sigma <- 9.40053189984482                     # 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(3554486)
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 = 145 (80% power), 194 (90% power)
 75% of observed effect: n per arm = 257 (80% power), 344 (90% power)
 50% of observed effect: n per arm = 578 (80% power), 773 (90% power)
power.t.test: 145.3 
Simulated power at n = 145 per arm: 0.801 (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 two-sided t-test as p = 0.051 for the comparison of Fiasp and Novolog. It does not give the sponsor’s treatment-effect estimate or confidence interval, nor does it specify whether the test accounted for the crossover pairing, sequence, or period. As a result, the sponsor’s reported p-value cannot be fully interpreted from the record alone.

The separate unadjusted recalculation gives a Novolog-minus-Fiasp mean difference of -3.1 percentage points, a 95% confidence interval from -9.078 to 2.878, and p = 0.309. That recalculation is based on the posted summary statistics and should not be treated as a reproduction of the sponsor’s analysis. The two p-values are different, and the registry record does not explain why; it does not provide enough information to determine whether their methods or assumptions differ.

The sponsor’s analysis remains the study’s reported analysis, while the recalculation offers a transparent summary-statistic comparison. Neither p-value alone describes the magnitude and precision as fully as an estimate with an interval. The registry record does not report a reconciliation, so readers should keep the two results clearly attributed to their respective analyses rather than combine them or select one without regard to its method.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and posts a secondary outcome, but does not report a statistical analysis plan or a multiplicity strategy. It is therefore not reported in the registry record whether the secondary analysis was intended to be confirmatory, whether outcomes were tested in a prespecified order, or whether p-values were adjusted for multiple comparisons. In general, multiplicity matters because conducting several statistical tests can increase the chance of obtaining at least one apparently notable result by chance. Unadjusted secondary results should consequently be interpreted cautiously.

The primary analysis population is described as participants who completed the protocol. The registry lists enrollment of 27, while the treatment summaries report 19 observations for each insulin condition. It does not provide a participant flow diagram or explain the reasons for non-completion, exclusions, or the difference between enrollment and the reported outcome denominators. The exact handling of missing sensor readings and incomplete treatment periods is also not reported in the registry record.

These details matter because missing data can affect both the estimate and its uncertainty, particularly if the chance of missingness is related to glucose measurements, treatment period, or participant characteristics. In general, complete-case analyses can differ from analyses that make other assumptions about missing observations. The registry’s description of protocol completers does not establish how partial sensor records were handled or whether any sensitivity analyses were conducted.

The record reports a two-sided t-test for the sponsor’s analyses, but does not specify whether the primary comparison was paired, whether period or sequence effects were considered, or how the crossover design was represented. Those methods are not reported in the registry record. Without those details, readers cannot verify the analysis population, assumptions, or multiplicity handling, and should avoid treating the posted summaries as a complete account of the statistical plan.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infusion set failure (5.3%).

The safety summaries report no serious adverse events in the run-in period, with 28 at risk, or in the Fiasp period, with 19 at risk. In the Novolog period, with 19 at risk, the registry reports one participant affected by a serious adverse event. It reports no deaths in any of these periods. The record also lists infusion set failure at 5.3% among the top serious-event terms; it does not provide enough detail in this summary to establish how that term relates to the event counts by treatment period.

The registry also reports one participant affected by an other adverse event in the Novolog period, and none in the run-in or Fiasp periods. These are descriptive counts in a small pilot study, not a reliable basis for comparing uncommon harms. The record does not provide detailed event narratives, exposure-adjusted rates, or a causal assessment in the posted summary. In general, adverse-event counts describe what was reported during observation; they do not alone establish that an insulin caused an event or that no unreported risk exists.

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

The results describe sensor-glucose outcomes during short treatment periods in a randomized, double-blind crossover pilot involving the 670G hybrid closed-loop system. The primary measure was the percentage of time sensor glucose values were between 70-180 mg/dl, summarized for a 7-day window during the second half of each intervention period. The posted group means and comparison are useful for understanding the observed data in this study population and setting.

The unadjusted recalculation estimates a difference in means, but its confidence interval is broad enough to include zero and values on either side. The sponsor’s reported p-value is different, and the registry does not report enough methodological detail to reconcile the analyses. Together, these limitations mean that the posted results should be read as preliminary and analysis-dependent, not as a definitive estimate of the treatment contrast.

The study does not establish equivalence between Fiasp and Novolog: the registry does not report a prespecified equivalence margin or an analysis designed to establish equivalence. Nor does a nonsignificant recalculated result prove that no difference exists. A lack of compelling evidence in this analysis is not evidence that every potentially important difference has been excluded.

The results do not establish effects on outcomes not reported, long-term patterns, or pump modifications. The registry describes the study aim as obtaining preliminary information about Fiasp in a closed-loop system and determining whether pump changes might need to be made, but whether changes were needed is not reported in the registry record. The findings also cannot automatically be generalized beyond the participants, treatment schedule, system, and observation window described. The record’s limited details on missing data and crossover analysis further constrain interpretation.

18. Why This Trial Matters Statistically

This trial raises a central biostatistical issue: a crossover design generates repeated treatment observations from participants, so the relationship between a participant’s measurements can matter for estimating uncertainty. A simple comparison of posted group summaries is easy to interpret, but it may not represent the design-specific analysis. The registry does not provide enough detail to determine how its sponsor analysis handled that feature, making transparent reporting of the model and analysis population important.

The record also illustrates why estimates, confidence intervals, and p-values should be read together. A p-value alone does not show the size or precision of a difference. Here, the sponsor’s reported p-value and the unadjusted recalculation differ, while the sponsor’s estimate and interval are not reported. That leaves readers with an incomplete view of how the sponsor’s inference relates to the directly interpretable recalculated contrast.

Finally, the study is explicitly a pilot, and the sample-size figures are retrospective planning illustrations based on the observed effect rather than the trial’s own design. This distinction matters: a small preliminary study can inform what further evaluation might need to address, but its observed estimate may be unstable and should not be treated as a precise planning target without independent justification. Clear reporting of the crossover model, missing-data handling, multiplicity decisions, and rationale for the original sample size would help readers evaluate the strength and intended role of the evidence.

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.

The registry reports only a limited account of the statistical methods. It identifies the sponsor’s test as a two-sided t-test but does not state whether it was paired or how treatment sequence, period, or other crossover features were handled. The unadjusted recalculation is based on summary statistics, and the record does not provide the participant-level information needed to reproduce a crossover analysis or reconcile the reported p-values.

The primary population is described as participants who completed the protocol, but detailed participant flow and reasons for missing outcome data are not reported. The record also does not explain how incomplete sensor records were handled, whether exclusions were made, or whether sensitivity analyses were performed. These omissions make it difficult to assess whether the reported summaries represent all available measurements or a selected subset.

The study is described as a pilot, and the registry does not report the original sample-size justification or design assumptions. The planning illustrations based on the observed effect are not a substitute for that rationale. The record also does not report a multiplicity strategy, a prespecified hierarchy for secondary outcomes, or whether other planned measures were omitted from the posted results.

The endpoint covers a defined sensor-glucose window and does not, by itself, characterize longer-term outcomes or all aspects of system performance. The registry’s stated aim includes assessing whether pump changes might need to be made, but findings on that question are not reported in the registry record. These limitations are specific to the available description and results; they do not determine what may have been addressed in materials not included in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of Fiasp® (Fast Acting Insulin Aspart) in 670G Hybrid Closed-Loop Therapy — NCT03554486.
• Registry record last updated 2021-08-18; status last verified 2021-08.
• Results first posted 2021-08-18.
• 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

The registry record describes a completed randomized, double-blind, crossover Phase 4 pilot of Fiasp and Novolog with the 670G hybrid closed-loop system in participants with type 1 diabetes. After a 2-week run-in, participants used each insulin for 2 weeks in one of two sequences. The primary endpoint was percentage of time with sensor glucose between 70-180 mg/dl, assessed over 7 days during the second half of each intervention period.

The reported primary means are 78.4% for Fiasp and 75.3% for Novolog. The unadjusted recalculation gives a Novolog-minus-Fiasp difference of -3.1 percentage points, with a 95% confidence interval from -9.078 to 2.878 and p = 0.309. The sponsor’s reported two-sided t-test has p = 0.051; the registry does not explain the difference between analyses. The sponsor’s effect estimate, crossover analysis details, missing-data methods, and original sample-size rationale are not reported in the registry record.