Optimizing Electronic Alerts for Acute Kidney Injury: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Optimizing Electronic Alerts for Acute Kidney Injury (NCT02753751), a randomized na study. The primary outcome is Composite of Progression of AKI, Inpatient Dialysis, or Inpatient Death.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group study with triple masking. It lists the phase as not applicable and the study status as completed. Yale University is listed as the sponsor. The recorded enrollment is 6030. The study start date is 2018-03-26, and the primary completion date is 2020-01-06. The registry does not identify which people or groups were masked, so the practical meaning of triple masking for clinicians, participants, outcome assessors, or analysts is not reported in the registry record.

Participants were assigned to usual care or the electronic acute kidney injury alert. Usual care involved no alert being fired. In the alert group, a pop-up was to fire when a provider opened the electronic health record of a patient with acute kidney injury, and to continue until acute kidney injury appeared in the problem list or resolved. The study is described as randomized, but the method used to generate or conceal the allocation sequence is not reported in the registry record. Details about sites, recruitment, adherence to the assigned approach, crossover, and co-interventions are also not reported in the registry record.

The primary endpoint covered the 14 days from randomization. The registry lists eight secondary outcomes, including mortality, dialysis, acute kidney injury progression, duration, readmission, index hospitalization cost, best-practice attainment, and chart documentation of acute kidney injury. Results are posted for mortality, dialysis, and acute kidney injury progression; results for the other listed secondary outcomes are not reported in the registry record. The registry does not describe the original sample-size justification or the trial's detailed analysis plan. Randomization supports a comparison between assigned groups, but interpretation also depends on the handling of missing observations, analysis populations, and the extent to which the assigned alert was delivered as intended; those details 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.

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 Composite of Progression of AKI, Inpatient Dialysis, or Inpatient Death, measured over 14 days from randomization.

The primary endpoint counts participants who experienced at least one event in a composite of acute kidney injury progression, inpatient dialysis, or inpatient death during the 14 days from randomization. Progression was defined as an increase in KDIGO creatinine stage from the stage present at randomization. Dialysis included hemodialysis, continuous renal replacement therapy, or peritoneal dialysis; isolated ultrafiltration for volume removal was excluded. Mortality was determined from hospital administrative records.

As a general statistical rationale, a composite endpoint can bring several clinically relevant events into a single outcome and may capture more participants with an event than any one component alone. Its interpretation depends on the component definitions and on whether the components are understood as sufficiently relevant to the question. A composite does not show whether the groups differ in each component, and a result driven by one component can have a different meaning from a result driven by another. Component-level results are therefore useful alongside the combined endpoint. Mortality, dialysis, and acute kidney injury progression are also listed as secondary outcomes, but the registry does not report component-specific analyses of how each contributed to the primary composite.

The reported primary outcome is a count of participants with an event, rather than a time-to-event measure or a continuous measure of kidney function. The registry gives a common follow-up window of 14 days from randomization for the primary endpoint. Whether all participants had complete follow-up over that period, and how incomplete follow-up was handled, is not reported in the registry record.

7. Results Posted in the Registry

• Electronic AKI Alert: 21.3% (653/3059) versus 20.9% (622/2971) on control; risk difference 0.4 percentage points (95% CI -1.7 to 2.5), risk ratio 1.02 (0.92–1.12); unadjusted two-proportion z-test p = 0.696.

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.

Mortality

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Electronic AKI Alert: 8.9% (272/3059) versus 8.9% (265/2971) on control; risk difference -0.0 percentage points (95% CI -1.5 to 1.4), risk ratio 1.00 (0.85–1.17); unadjusted two-proportion z-test p = 0.970.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Electronic AKI Alert and the control. The interval gives the range of effects that remain compatible with the data.

Dialysis

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Electronic AKI Alert: 3.5% (106/3059) versus 3.1% (93/2971) on control; risk difference 0.3 percentage points (95% CI -0.6 to 1.2), risk ratio 1.11 (0.84–1.46); unadjusted two-proportion z-test p = 0.467.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Electronic AKI Alert and the control. The interval gives the range of effects that remain compatible with the data.

AKI Progression

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Electronic AKI Alert: 15.9% (487/3059) versus 15.5% (461/2971) on control; risk difference 0.4 percentage points (95% CI -1.4 to 2.2), risk ratio 1.03 (0.91–1.15); unadjusted two-proportion z-test p = 0.667.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Electronic AKI Alert and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists eight secondary outcomes, including mortality, dialysis, acute kidney injury progression, acute kidney injury duration, readmission rate, index hospitalization cost, best-practice attainment, and chart documentation of acute kidney injury. Detailed results are posted for mortality, dialysis, and progression. Results for duration, readmission, cost, best-practice attainment, and documentation are not reported in the registry record.

Across the three secondary outcomes with posted comparisons, the unadjusted point estimates are close to their no-difference reference values, and each confidence interval includes the no-difference value for its measure. This broad pattern is consistent with the primary comparison's lack of strong statistical evidence for a difference. It does not establish that every outcome is unaffected or that the component outcomes and composite have the same interpretation. The individual estimates and intervals should be read from their displayed results rather than inferred from the combined endpoint.

Secondary outcomes are generally less definitive than a prespecified primary comparison when many outcomes are examined. Each additional comparison creates another opportunity for a result to appear unusual by chance. The registry does not report whether a multiplicity adjustment was planned or used, or how the secondary outcomes were ranked for interpretation. As a result, unadjusted secondary p-values, where reported in recalculations, should be treated as exploratory rather than as independent confirmatory evidence. The registry's posted secondary results do not include sponsor analyses for these outcomes.

The secondary outcomes can nevertheless help describe the clinical pattern and identify questions for further study. Their evidential weight depends on the analysis plan, completeness of outcome collection, prespecification, and precision. These details are not fully reported in the registry record. In particular, the absence of posted results for some listed outcomes means that no conclusion about those outcomes can be drawn from the registry record.

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

• Mortality
• Dialysis
• AKI Progression
• AKI Duration
• Readmission Rate
• Index Hospitalization Cost
• Proportion of AKI "Best Practices" Achieved Per Subject During Index Hospitalization
• Number of Subjects With Chart Documentation of AKI

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in the comparison group. It is an absolute contrast: zero corresponds to equal event proportions. The recalculated primary risk difference is 0.004, with a 95% confidence interval from -0.017 to 0.025. Because the interval crosses zero, the posted summary statistics are compatible with no absolute difference as well as with differences in either direction. A risk difference can be easier to relate to absolute event frequency than a relative measure, but its interpretation depends on the outcome definition and follow-up period.

What does the risk ratio describe?

A risk ratio divides one group's event proportion by the other's. A value of 1 corresponds to equal event proportions; values on either side indicate relative differences in opposite directions. The sponsor's reported primary risk ratio is 1.02, with a 95% confidence interval from 0.93 to 1.13. That interval includes 1. The unadjusted recalculation reports a risk ratio of 1.02, with a confidence interval from 0.925 to 1.124. These are different reported analyses and intervals, so they should not be treated as identical calculations.

What does the confidence interval add?

A confidence interval conveys uncertainty around an estimate under the assumptions of the statistical method. It is more informative than a point estimate alone because it shows a range of values reasonably compatible with the data under that method. A wider interval indicates less precision than a narrower interval on the same scale. The interval does not represent the probability that the true effect falls within that particular range, and it does not account automatically for limitations such as missing data, outcome measurement, or selective reporting.

How should the p-value be read?

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, and it does not quantify clinical importance. The registry's reported primary analysis gives p = 0.67; the unadjusted recalculation gives p = 0.696. These are not the same analysis and should be read in their respective contexts. Neither p-value, by itself, establishes that the groups are identical or that a clinically meaningful difference is absent.

Why do the analysis methods matter?

The sponsor reports a Cochran-Mantel-Haenszel analysis of the risk ratio. This method can combine information across strata when a stratified analysis is specified. The registry does not report the stratification variables or enough detail to reconstruct the sponsor's procedure. The posted recalculation is a simple, unadjusted comparison from the summary counts. Because the methods differ, small differences in the estimates, intervals, and p-values are possible. The sponsor's reported result should be distinguished from the recalculation rather than replaced by it.

The primary endpoint is binary at the participant level: each participant is counted as having or not having the composite event within the stated follow-up period. The registry supplies participant counts by group. The general statistical properties of a binary comparison depend on the event frequency, the allocation, and the analysis assumptions. The registry does not report a detailed model specification beyond the sponsor's listed method, nor does it state how missing outcome information was treated.

Randomization is intended to make assigned groups comparable on average, including with respect to factors that may not be measured. It does not guarantee that every observed characteristic is balanced, and it does not resolve problems that can arise after assignment, such as non-adherence or missing outcomes. The record does not give details about baseline balance, the random sequence, concealment, or protocol deviations. Those omissions prevent a full assessment of these aspects of the trial methods from the registry record alone.

For an event-count endpoint, the analysis compares the number of participants with an event relative to the number in each group. It does not treat multiple events in one participant as multiple primary endpoint events. The composite's definitions matter because a participant can qualify through any of its components. General interpretation should keep the combined endpoint separate from each component and from outcomes not included in the composite.

The posted p-values and confidence intervals address sampling uncertainty under their respective calculations. They do not address the full range of uncertainty about generalizability, measurement, implementation, or study conduct. Statistical significance is not a measure of the size or importance of an effect; likewise, a result that is not statistically significant does not establish the absence of an effect.

11. Confidence Intervals and Precision

The sponsor's primary risk-ratio estimate is 1.02, with a 95% confidence interval from 0.93 to 1.13. The interval includes 1, the reference value for no relative difference. Its bounds allow for a relative effect in either direction around the point estimate. The registry does not report an equivalence margin or another threshold for deciding what range of effects would be clinically unimportant, so the interval cannot be used to make a formal equivalence claim.

The unadjusted recalculation gives a risk difference of 0.004, with a 95% confidence interval from -0.017 to 0.025. This interval includes zero, the reference value for no absolute difference. The risk-difference interval gives the uncertainty on an absolute scale, while the sponsor's risk-ratio interval gives it on a relative scale. Both intervals indicate that the point estimates should not be read as precise evidence of a difference.

Confidence intervals are sensitive to the analysis method and assumptions. The sponsor's Cochran-Mantel-Haenszel result and the unadjusted recalculation are not identical analyses. The registry does not report the stratification details for the sponsor's method or the handling of missing data, so the posted information does not permit a complete appraisal of all sources of uncertainty. A confidence interval also does not cover possible bias from outcome measurement, implementation, or selective reporting.

In general, interval width is a practical guide to statistical precision: a narrower interval indicates greater precision on its scale, while a wider interval leaves more uncertainty about the size and direction of the effect. Precision is distinct from clinical importance. Interpreting importance would require a clinical threshold, and such a threshold is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculation. For the binary outcomes, the figures are participants per arm, not total participants. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect were present. The 90% power column gives the corresponding planning number for a 90% chance. These are planning targets, not guarantees that a study of that size will produce a particular result. The primary-outcome illustration includes planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. As the target effect becomes smaller, more participants are needed to distinguish it from random variation under the same assumptions. The plotted relationship should be read in that general way: smaller target effects require larger sample sizes.

For the primary endpoint, the illustration gives 154,829 participants per arm for 80% power and 207,271 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 274,761 and 367,827 participants per arm. For 50% of the observed effect, they are 617,109 and 826,133 participants per arm. These values describe hypothetical planning scenarios; they are not a statement of the trial's actual design target. This is not observed power.

Planning figures depend on the assumed effect, significance level, allocation, and approximation. In practice, the effect used for planning is uncertain, and an effect estimated from a completed study may be unstable. The illustrations should therefore be read as conditional calculations, not as evidence that the trial was underpowered or that any particular effect is present.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.209; treatment proportion p₁ = 0.213; average p̄ = 0.211.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5774 = 1.1318.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5774 = 0.4860.
4. n = (1.1318 + 0.4860)² / (0.0041)² = 154,828.0, rounded up to 154,829 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
p0 <- 0.209357118815214                          # control proportion
p1 <- 0.213468453743053                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2753751)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 154,829 (80% power), 207,271 (90% power)
 75% of observed effect: n per arm = 274,761 (80% power), 367,827 (90% power)
 50% of observed effect: n per arm = 617,109 (80% power), 826,133 (90% power)
power.prop.test: 154828 
Simulated power at n = 154,829 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 sponsor's posted primary analysis uses the Cochran-Mantel-Haenszel method and reports a risk ratio of 1.02, a 95% confidence interval from 0.93 to 1.13, and p = 0.67. The recalculation from the posted group counts is an unadjusted analysis, expressed as a risk difference of 0.004, a 95% confidence interval from -0.017 to 0.025, and p = 0.696. The sponsor's analysis and the recalculation use different measures and methods, so their estimates and p-values are not directly interchangeable.

The registry does not mark a discrepancy between the posted sponsor result and the recalculation. The sponsor's result is the reported trial analysis; the recalculation is a separate, simple comparison of the summary counts. The registry does not provide the strata or other details needed to reproduce the sponsor's method fully. Accordingly, the reported sponsor analysis is the appropriate description of the registry's own primary analysis, while the recalculation offers a complementary unadjusted view of the posted counts.

Both analyses have intervals that include the respective no-difference value. Their results therefore do not provide strong statistical evidence of a primary-outcome difference. That shared qualitative reading does not make the methods equivalent, nor does it establish that the groups have identical outcomes.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, but does not report whether the study used a multiplicity strategy. It is not reported in the registry record whether the investigators adjusted significance thresholds or p-values for testing multiple outcomes, specified a hierarchy among secondary outcomes, or controlled a family-wise error rate. Without that information, secondary comparisons should not be treated as though each were a separately confirmed primary result. A general reason for caution is that examining many outcomes increases the chance of observing an apparently unusual result by chance.

The registry does not report how missing outcome data were handled, whether any participants were excluded from the primary analysis, or the analysis population used for the reported comparison. It is not reported in the registry record whether the primary analysis followed intention-to-treat principles, a per-protocol approach, or another population definition. The group counts are posted, but the record does not explain whether these represent all randomized participants with complete outcome information or how incomplete follow-up was addressed.

These omissions matter because analysis choices can affect the interpretation of randomized comparisons. If outcome information is incomplete, the method used to handle it can influence the estimate and its uncertainty. If the analyzed population differs from the randomized population, the comparison may no longer preserve all the benefits of randomization. The registry does not provide enough detail to assess those possibilities.

The registry also does not report interim analyses, stopping rules, a detailed statistical analysis plan, or whether any changes were made to the planned analyses. These matters are not evidence that such procedures were or were not used; they are simply not reported in the registry record. The conclusions should be based on the analyses and outcomes that are posted, with the limits of that reporting kept in view.

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.

The adverse-event record lists zero serious adverse events and zero other adverse events in both groups. The corresponding at-risk counts are 2971 for usual care and 3059 for the electronic alert. The record lists 265 deaths in usual care and 272 in the alert group. It does not list serious adverse-event terms.

These figures should be read as registry-reported counts, not as a complete safety evaluation. The record does not describe the adverse-event collection procedures, definitions, attribution, observation window, or whether reporting was complete. The primary composite also includes inpatient death, but the safety listing is a separate registry record and should not be assumed to use identical analysis rules. The counts alone do not establish a causal relationship with the alert or indicate the clinical circumstances of the events.

Zero recorded adverse events in a category does not show that no events occurred outside the reporting process or that all possible harms were assessed. Interpretation depends on how events were sought, defined, and recorded, details that are not reported in the registry record. These figures therefore describe what the registry lists and do not support broader safety conclusions.

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

The posted primary analysis compares assignment to an electronic acute kidney injury alert with assignment to usual care among hospitalized adults with acute kidney injury. The primary endpoint was a composite of acute kidney injury progression, inpatient dialysis, or inpatient death during the 14 days from randomization. The sponsor's reported risk ratio is 1.02, with a 95% confidence interval from 0.93 to 1.13 and p = 0.67. The unadjusted recalculation also has an interval that includes no difference.

These results do not provide strong statistical evidence of a difference between the assigned groups on the primary composite. They do not prove that the groups are identical, rule out every potentially meaningful effect, or establish equivalence. No clinical threshold for a meaningful difference is reported in the registry record. The confidence interval represents uncertainty under the analysis method and does not capture every possible source of uncertainty or bias.

The composite result does not, on its own, explain the outcome pattern for progression, dialysis, or death. Secondary results are available for those outcomes, but they are separate analyses, and the registry does not report results for all listed secondary outcomes. Nor does the primary endpoint measure every possible consequence of an alert, such as changes in clinical processes, unless captured by the listed outcomes.

The result applies most directly to the randomized comparison recorded in this trial. Details about study sites, implementation, adherence, missing data, and analysis populations are not reported in the registry record, which limits assessment of how the result might apply in other settings or under different alert workflows. The findings should be understood as evidence about the posted outcomes and analyses, not as a general recommendation about clinical practice.

18. Why This Trial Matters Statistically

This trial addresses a statistical challenge common in evaluations of electronic alerts: the intervention is a change in information delivered through a clinical system, while the outcomes of interest occur downstream in patient care. A randomized comparison can help separate the effect associated with assignment to an alert from differences that might otherwise distinguish groups. The registry identifies a parallel randomized design and describes the alert's trigger and stopping conditions, giving readers a basis for understanding the contrast.

The primary endpoint combines acute kidney injury progression, dialysis, and inpatient death. Composite outcomes can summarize several events in one analysis, but they require careful interpretation because a single overall estimate may conceal different patterns among components. The registry also lists component-related secondary outcomes, making clear why readers should consider both the combined endpoint and the component results rather than relying on one summary alone.

The trial also illustrates the importance of distinguishing a sponsor's reported analysis from a simple unadjusted recalculation. The sponsor reports a risk ratio using a Cochran-Mantel-Haenszel method, while the recalculation expresses the group contrast as a risk difference. Both are useful descriptions, but they answer on different scales and are based on different procedures. Keeping those distinctions visible supports a more accurate reading of the estimates.

Finally, the confidence intervals show why a non-significant result should not be treated as proof of no effect. The estimates have uncertainty, and the registry does not provide a clinical threshold for judging which effects would matter. Reading the point estimates, intervals, endpoint definitions, and reporting gaps together gives a more disciplined account than relying on a p-value alone.

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 record gives the core design and outcome information but leaves important methodological details unreported. The randomization sequence and allocation concealment are not described, and the meaning of triple masking is not specified. Study sites, eligibility details beyond hospitalized adults with acute kidney injury, and baseline characteristics are not reported in the registry record. These omissions limit assessment of recruitment, setting, and the practical scope of the comparison.

Information about implementation is also limited. The alert's trigger and stopping conditions are described, but alert delivery, clinician response, adherence, crossover, and co-interventions are not reported. Without these details, the comparison is best understood as one between assigned strategies, not necessarily between consistent receipt and non-receipt of the alert.

The record does not report the original sample-size rationale, analysis populations, missing-data methods, interim analyses, or a detailed statistical analysis plan. It also does not report whether multiplicity was addressed. These gaps make it difficult to assess the prespecification and completeness of the statistical analyses. Results are posted for only some of the listed secondary outcomes; results for the others are not reported in the registry record.

The primary endpoint depends on several component definitions and includes mortality determined from hospital administrative records. The registry does not provide further information about outcome adjudication or completeness of follow-up. Safety reporting lists zero serious and other adverse events in both groups but does not describe ascertainment methods or the observation window. These limitations do not negate the posted findings, but they constrain how fully the trial can be evaluated from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Optimizing Electronic Alerts for Acute Kidney Injury — NCT02753751.
• Registry record last updated 2022-02-10; status last verified 2022-01.
• Results first posted 2022-02-10.
• 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 describes a completed, randomized, triple-masked, parallel-group study sponsored by Yale University, with enrollment of 6030. It compared usual care, with no alert, against an electronic alert for hospitalized adults with acute kidney injury. The alert was to appear when a provider opened the patient's electronic health record and to continue until acute kidney injury was documented in the problem list or resolved.

The primary endpoint was a 14-day composite of acute kidney injury progression, inpatient dialysis, or inpatient death. The sponsor's Cochran-Mantel-Haenszel analysis reports a risk ratio of 1.02, with a 95% confidence interval from 0.93 to 1.13 and p = 0.67. The unadjusted recalculation also has a confidence interval that includes no difference. The registry lists eight secondary outcomes, with results posted for mortality, dialysis, and progression. Important details about missing data, analysis populations, multiplicity, and the original sample-size rationale are not reported in the registry record.