Telemedicine Control Tower for the Operating Room: Navigating Information, Care and Safety: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Telemedicine Control Tower for the Operating Room: Navigating Information, Care and Safety (NCT03923699), a randomized phase 3 study. The primary outcome is Thirty-day Postoperative Mortality.

2. Clinical Question

The question concerns whether the monitoring approach was associated with a different recorded risk of death within the specified postoperative period. It is a comparison of two assigned care strategies in a randomized, parallel-group trial, not a comparison of monitoring with no operating-room monitoring: the standard-of-care rooms were also monitored, with contact restricted to circumstances judged clinically necessary for patient safety. The contrast therefore concerns the additional support and monitoring strategy described for the Control Tower arm.

The registry lists 79,560 participants and reports the trial as completed. It describes the study as a randomized pragmatic trial and lists surgery and surgical complications among its conditions. It does not report a more specific eligibility population in the primary-outcome description, nor does it specify in the record how participants or operating rooms were selected for inclusion. The result should consequently be read as a comparison within the registry-defined trial population, rather than assumed to apply to every surgical setting or patient group.

3. Trial Design

The registry describes a Phase 3, randomized, single-masked, parallel trial. Enrollment was 79,560. The record lists Washington University School of Medicine as sponsor and reports the study as completed. The listed study dates are 2019-07-01 for start and 2023-01-31 for primary completion. The title identifies the study as a randomized pragmatic trial.

The two arms were standard of care and Anesthesia Control Tower monitoring. The standard-of-care arm included operating-room monitoring, with ACT clinicians contacting the room only when clinically necessary for patient safety. In the monitoring arm, Anesthesiology Control Tower clinicians were to provide extra support to the operating-room anesthesiology team using AlertWatch and integrating machine-learning forecasting algorithms for adverse outcomes. This arm distinction is important: the comparison is between usual monitoring with restricted contact and a described additional-support strategy, not simply between surveillance and no surveillance.

The primary endpoint was a count of participants who died from any cause within 30 days after index surgery, whether the death occurred in or out of hospital. The posted arm counts were 899 of 39,750 in standard care and 866 of 39,810 in Control Tower monitoring. The analysis record identifies a Poisson regression for the sponsor-reported risk ratio. The specific model covariates, details of the randomization procedure, masking identity, and analysis population are not reported in the registry record.

The record lists 11 outcome measures and 11 analyses. Its secondary outcomes include temperature management, antibiotic redosing, mean arterial pressure management, mean airway pressure with mechanical ventilation, blood glucose management, measured anesthetic concentration, and fresh gas flow rates. The registry record does not describe the original sample-size justification, allocation implementation, interim analyses, or detailed statistical analysis plan. These omissions limit what can be inferred about how the trial was planned and how all outcomes were evaluated.

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 Thirty-day Postoperative Mortality, measured over 30 days post-op.

The primary endpoint, Thirty-day Postoperative Mortality, counts participants who died from any cause within 30 days of the index surgery. The definition includes deaths occurring either in or out of hospital. It is a binary participant-level outcome: each participant is classified according to whether a qualifying death occurred during the stated follow-up period.

Mortality is used as a direct, clinically important outcome in this trial because the intervention is intended to support perioperative care and the registry frames the research around adverse outcomes and patient safety. A fixed follow-up window gives the endpoint a defined period over which deaths are counted. Including deaths outside hospital means ascertainment is not restricted to events occurring during the surgical admission, according to the registered definition.

The endpoint captures only deaths within the specified period. It does not, by itself, describe complications that did not result in death, timing within the 30-day period, cause of death, or longer-term outcomes. Those features are not part of the primary-endpoint definition in the registry record. The posted result is therefore an arm comparison for the occurrence of death during the defined window, not a full account of all postoperative outcomes or of the pathway leading to any death.

7. Results Posted in the Registry

• Anesthesia Control Tower Monitoring: 2.2% (866/39810) versus 2.3% (899/39750) on control; risk difference -0.1 percentage points (95% CI -0.3 to 0.1), risk ratio 0.96 (0.88–1.05); unadjusted two-proportion z-test p = 0.409.

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.

Temperature Management

• 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:
  • Anesthesia Control Tower Monitoring: 78.9% (27398/34711) versus 78.9% (27101/34340) on control; risk difference 0.0 percentage points (95% CI -0.6 to 0.6), risk ratio 1.00 (0.99–1.01); unadjusted two-proportion z-test p = 0.969.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Anesthesia Control Tower Monitoring and the control. The interval gives the range of effects that remain compatible with the data.

Antibiotic Redosing

• 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:
  • Anesthesia Control Tower Monitoring: 95.1% (5629/5919) versus 95.0% (5520/5811) on control; risk difference 0.1 percentage points (95% CI -0.7 to 0.9), risk ratio 1.00 (0.99–1.01); unadjusted two-proportion z-test p = 0.787.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Anesthesia Control Tower Monitoring and the control. The interval gives the range of effects that remain compatible with the data.

Mean Arterial Pressure Management

• 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:
  • Anesthesia Control Tower Monitoring: mean 0.96 versus 0.96 on control; difference 0.00 (95% CI -0.00 to 0.00), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Anesthesia Control Tower Monitoring and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists several secondary outcomes covering perioperative management processes, including temperature management, antibiotic redosing, mean arterial pressure management, mean airway pressure with mechanical ventilation, blood glucose management, measured anesthetic concentration, and fresh gas flow rates. The posted detailed comparisons available for temperature management, antibiotic redosing, and mean arterial pressure management have estimates close to their respective no-difference values, and their confidence intervals include those values. At an overall level, these results do not show a clear separation between the arms in the available secondary comparisons.

This broad pattern is consistent with the primary result in the limited sense that neither set of posted comparisons demonstrates a clear difference. It does not serve as confirmation of the primary finding, nor does it establish that all aspects of perioperative management were unchanged. Secondary endpoints address different processes, may involve different numbers of participants, and do not necessarily represent the same clinical question as mortality. Detailed results for the other listed secondary outcomes are not reported in the registry record.

Unadjusted secondary findings deserve less weight when many outcomes are assessed because the chance of observing apparently notable results can increase as the number of comparisons grows. In general, multiplicity procedures can control that issue, but the registry record does not report a multiplicity adjustment or a hierarchy of secondary hypotheses. Without those details, individual secondary p-values should be treated as exploratory rather than as stand-alone confirmatory evidence. The overall direction and precision of the available estimates are more informative than selectively emphasizing an isolated result, but even that pattern must be interpreted within the reported endpoints and missing analysis details.

The secondary outcomes may help describe how the strategies related to recorded care processes, but they do not replace the primary endpoint or resolve its uncertainty. The record does not report a prespecified strategy for interpreting the secondary outcomes collectively, nor does it describe how missing measurements were handled for each outcome. That limits claims about the completeness and comparative importance of the full secondary-outcome set.

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

• Temperature Management
• Antibiotic Redosing
• Mean Arterial Pressure Management
• Mean Airway Pressure With Mechanical Ventilation
• Blood Glucose Management
• Measured Anesthetic Concentration
• Fresh Gas Flow Rates

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, the outcome is binary at the participant level: a participant either had a qualifying death within the registered 30-day window or did not. The posted counts and arm sizes allow an unadjusted comparison of the proportions. The recalculated risk difference expresses the absolute contrast between those proportions. Its estimate is -0.001, with a 95% confidence interval from -0.003 to 0.001. A risk difference of 0 represents no absolute difference, so an interval spanning 0 includes that possibility.

The registry's sponsor-reported analysis uses Poisson regression and reports a risk ratio. A risk ratio compares the event risk in one arm with the event risk in the comparator arm on a relative scale. A risk ratio of 1 represents equal risks; values below or above 1 indicate a lower or higher estimated risk in the intervention arm relative to the comparator. The posted estimate is 0.96, with a 95% confidence interval from 0.85 to 1.08. Because this interval includes 1, it includes no relative difference as well as values on either side of that reference point. The regression model's covariates and other implementation details are not reported in the registry record.

What does a confidence interval communicate?

In general, a confidence interval represents uncertainty around an estimated effect under the statistical method used. It is not a guarantee that the true effect lies within the particular interval, nor does it give the probability that the treatment effect is exactly a particular value. The interval communicates a range of effects compatible with the data and method at the stated confidence level. Wider intervals indicate less precision; narrower intervals indicate more precision. For the primary endpoint, the reported interval includes the no-difference value, so the posted data do not distinguish clearly between no relative difference and effects in either direction within the interval.

How does the recalculation differ from the sponsor analysis?

The recalculated comparison is an unadjusted risk difference based on the posted summary statistics. It does not reproduce a regression model or account for covariates that might have been included in the sponsor's analysis. The sponsor reported a regression-based risk ratio. These are distinct estimands and scales: one gives an absolute difference and the other a relative comparison. Their numerical values should not be compared as though they measured the same quantity. The registry record does not flag a discrepancy, and the sponsor-reported analysis remains the recorded regression result.

For the secondary outcomes, the registry lists both binary outcomes and a continuous measure. A binary outcome counts participants meeting the stated condition, whereas a continuous outcome is summarized by a mean and standard deviation. The mean arterial pressure management result is expressed as percentage of time, with a mean of 0.96 and standard deviation of 0.08 in each arm. The posted unadjusted mean difference is 0.0, with a 95% confidence interval from -0.001 to 0.001. The sponsor analysis for this outcome reports a linear regression estimate for mean difference, with a 95% confidence interval from -0.00 to 0.00 and p = 0.29. The model details are not reported.

Why can over-dispersion matter?

In general, count and binary-outcome models rely on assumptions about how variability relates to the mean. Over-dispersion occurs when the observed variability is greater than the model expects. If not addressed, estimated uncertainty can be too small, making confidence intervals too narrow and tests too optimistic. Whether over-dispersion was assessed or addressed in the Poisson regression for this trial is not reported in the registry record. The word Poisson in the recorded method alone does not establish which diagnostics or variance adjustments were used.

The trial is described as randomized, single-masked, and parallel. Randomization is intended to support a fair comparison by assigning participants or units to different strategies, while a parallel design compares groups assigned to different arms over the same trial period. The registry record does not specify the randomization unit, masking identity, allocation concealment, or analysis population. Therefore, those design features cannot be elaborated beyond the labels recorded. No particular interim analysis, covariate adjustment plan, or missing-data approach should be inferred from the trial label or from the reported model name.

All inferential statements should distinguish a failure to show a clear difference from proof that the strategies are identical. A conventional superiority analysis asks whether the data provide evidence of a difference in a specified direction or either direction, depending on the test. The registry identifies the reported analyses as superiority analyses. It does not report a non-inferiority or equivalence design, nor margins for such a claim. Accordingly, the confidence intervals and p-values should be read as estimates and tests within the posted superiority analyses, not as evidence that the arms meet an equivalence criterion.

11. Confidence Intervals and Precision

The primary risk-ratio estimate is 0.96, with a 95% confidence interval from 0.85 to 1.08. This interval spans the no-relative-difference value of 1. It is compatible with lower and higher relative risks in the monitoring arm, so the central estimate alone should not be read as a settled effect. The p-value of 0.41 is consistent with the interval's inclusion of the null value under the reported analysis.

On the absolute scale, the recalculated risk difference is -0.001, with a 95% confidence interval from -0.003 to 0.001. This interval spans 0, the no-absolute-difference value. It expresses uncertainty in the unadjusted difference calculated from the posted arm summaries. It does not have the same scale or necessarily the same adjustment as the sponsor's regression estimate.

Precision is about the range of effects compatible with the data, not simply whether a test crosses a threshold. The primary confidence intervals do not isolate one direction of effect. They therefore leave uncertainty about whether the true contrast is a small benefit, little or no difference, or a small harm on the relevant scale. The registry record does not provide a prespecified threshold for a clinically important difference, so the intervals cannot be classified against such a threshold from the record alone.

The number of participants enrolled is large, but a large enrollment does not make every possible effect estimate precise enough to rule out small differences. Precision depends on the outcome frequency, the effect size, the analysis, and variability. The registry's observed estimates and their intervals are the appropriate basis for describing precision; planning calculations based on the observed effect do not change the uncertainty in the actual trial result.

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 illustrations are planning calculations based on the observed effect, not the trial's original design assumptions. The registry record's description of the original sample-size justification is not reported in the registry record. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

For these outcomes, the figures are participants per arm. The event-count convention for time-to-event calculations does not apply to these participant-level outcomes. A per-arm figure is the planned number for one group under the stated assumptions, not the total across both groups. The planning columns describe the number of participants per arm associated with 80% or 90% power for the assumed effect. In plain terms, power is the probability that a specified analysis would detect the assumed effect at the stated significance level if that effect were the true one and the assumptions held. The 90% column targets a higher probability of detection than the 80% column, and therefore calls for a larger planned sample under otherwise matching assumptions.

The rows use the observed effect or a stated fraction of it. Planning for a smaller effect requires more participants because a smaller signal is harder to distinguish from sampling variation. The figures can be very large where the observed difference is close to zero; those values illustrate the consequences of planning around effects of that size under the specified assumptions. They are not evidence that the trial enrolled those numbers, nor do they establish what effect the trial was designed to detect. These calculations are not observed power: they are prospective-style planning illustrations based on the recorded estimate, not a measure of the trial's achieved evidence or a substitute for interpreting confidence intervals.

These calculations also depend on their assumptions. Equal allocation, the normal approximation, and the chosen effect fraction define the illustration; actual design considerations may differ. The registry record does not report whether these assumptions match the original protocol. The values should therefore be read as conditional planning quantities, not as a retrospective judgment about whether the trial was appropriately sized.

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 = 0.023; treatment proportion p₁ = 0.022; average p̄ = 0.022.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2083 = 0.4082.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2083 = 0.1753.
4. n = (0.4082 + 0.1753)² / (-0.0009)² = 457,197.6, rounded up to 457,198 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 <- 0.0226163522012579                          # control proportion
p1 <- 0.02175332830947                          # 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(3923699)
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 = 457,198 (80% power), 612,058 (90% power)
 75% of observed effect: n per arm = 816,660 (80% power), 1,093,275 (90% power)
 50% of observed effect: n per arm = 1,846,173 (80% power), 2,471,501 (90% power)
power.prop.test: 457197.6 
Simulated power at n = 457,198 per arm: 0.804 (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-reported primary analysis is a Poisson regression with a risk ratio of 0.96, a 95% confidence interval from 0.85 to 1.08, and p = 0.41. The recalculation uses the posted arm counts and sizes to estimate an unadjusted risk difference of -0.001, with a 95% confidence interval from -0.003 to 0.001 and p = 0.409. The registry record does not flag a discrepancy between the posted analysis and recalculation.

The estimates are not interchangeable. The sponsor result is a relative effect from a regression analysis; the recalculation is an absolute difference from summary statistics and is unadjusted. Differences in scale and modeling mean the numerical estimates and intervals should not be expected to match. The sponsor's analysis is the analysis reported by the registry; the recalculation is a separate descriptive check derived from the arm summaries, not a replacement for that model.

Both analyses have intervals that include their respective no-difference values and neither provides a clear statistical separation between the arms. The sponsor-reported result should be read with its stated model and endpoint; the recalculated result offers a simple summary-scale comparison. The registry record does not report enough model detail to independently reproduce the regression analysis, including any covariates or variance adjustments that may have been used.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 11 outcome measures and 11 analyses and names multiple secondary outcomes. Testing several outcomes creates a multiplicity issue: even when there is no real effect, some comparisons may appear unusual by chance. In general, a prespecified hierarchy, adjustment procedure, or clearly designated exploratory analysis can help readers interpret a family of results. Whether the trial used such a strategy is not reported in the registry record. The posted secondary p-values therefore should not be interpreted as though the record establishes that they were adjusted for the full set of outcomes.

The registry identifies the reported analyses as superiority analyses, but a detailed statistical analysis plan is not reported in the registry record. The record does not state whether hypotheses were ordered, whether any interim analyses were planned or conducted, or how the primary and secondary outcomes were prioritized for formal inference. Those details should not be inferred from the number of listed outcomes or from the regression method reported for a particular analysis.

Missing-data methods and analysis populations are also not reported in the registry record. The arm sizes vary across the posted outcomes, but the record does not explain the reasons for those denominators, whether outcome measurements were unavailable, or how participants with missing values were treated. The analysis population for mortality is not explicitly described as intention-to-treat, per-protocol, or another population. The denominators should therefore be reported as posted rather than assigned an analysis-population label not present in the record.

Randomization supports causal interpretation when the trial is implemented and analyzed appropriately, but readers need details about allocation, follow-up, adherence, and analysis to evaluate possible bias. The registry identifies a randomized, single-masked, parallel design but does not report the masking identity, randomization unit, allocation concealment, or a full account of deviations from assigned strategy. These omissions do not prove that problems occurred; they limit what can be assessed from the registry record. The reported estimates remain interpretable as posted comparisons, with appropriate caution about unreported analysis and missing-data procedures.

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 39,750 participants at risk in standard care and 39,810 at risk in Anesthesia Control Tower monitoring. It records 0 participants affected by serious adverse events in each arm and 0 affected by other adverse events in each arm. The adverse-event listing contains no top serious-event terms. The death counts are 899 in standard care and 866 in monitoring, matching the primary mortality counts.

These entries should be read as the values recorded in the registry, not as proof that no adverse events occurred in the study. The record does not provide further details about adverse-event definitions, ascertainment, reporting completeness, severity categories beyond the listed fields, or the relationship between the zero affected counts and the deaths. Mortality is separately specified as the primary endpoint; the adverse-event fields do not replace that endpoint or explain the circumstances of the deaths.

The registry record does not provide an exposure-adjusted safety analysis, event narratives, or comparative safety model. The displayed affected counts alone cannot establish that the strategies had identical safety profiles. They provide a limited description of the adverse-event entries recorded for the two arms, and should be interpreted alongside the primary mortality outcome and the reporting limitations.

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

The registry result describes a randomized comparison of Anesthesia Control Tower monitoring with standard care for thirty-day postoperative mortality. The sponsor-reported risk ratio is 0.96, with a 95% confidence interval from 0.85 to 1.08 and p = 0.41. The unadjusted recalculated risk difference is -0.001, with a 95% confidence interval from -0.003 to 0.001 and p = 0.409. Both intervals include the value corresponding to no difference on their respective scales.

These results do not show a statistically clear difference between the arms in the posted primary analysis. That wording is not equivalent to proving there is no difference. The intervals retain uncertainty about effects in either direction, and the registry record does not provide a threshold for deciding which effects would be clinically important. Nor does the record report an equivalence or non-inferiority margin. The trial's superiority analysis should not be recast as a demonstration that the two strategies are equivalent.

The result also does not isolate the effect of operating-room monitoring versus no monitoring. Standard-care operating rooms were monitored, and ACT clinicians could make contact when clinically necessary for patient safety. The comparison concerns the additional support and monitoring strategy described for the Anesthesia Control Tower arm. The record does not report intervention frequency, adherence, or implementation details that would explain how the planned strategies were delivered in practice.

Finally, the findings apply to the trial population and outcomes as recorded. The primary outcome counts deaths from any cause within 30 days of index surgery, not all complications, longer-term outcomes, or every aspect of perioperative care. The listed secondary outcomes provide additional process measures, but their interpretation is constrained by missing detailed results and unreported multiplicity and missing-data methods. A complete assessment requires the scope of the endpoint, the precision of the estimate, and the limits of the registry record to be considered together.

18. Why This Trial Matters Statistically

Statistically, this trial illustrates why a large enrollment does not eliminate uncertainty about a treatment contrast. The primary analysis includes tens of thousands of participants in each arm, yet its confidence interval still spans the no-difference value and permits estimates on either side. The point estimate is only one part of the evidence; the interval communicates the range of effects that remains compatible with the analysis.

It also illustrates the importance of defining the comparator precisely. The standard-of-care group was monitored, with contact reserved for situations considered clinically necessary for patient safety. The intervention was a more active support approach involving Control Tower clinicians, AlertWatch, and machine-learning forecasting algorithms. Treating the comparison as monitoring versus no monitoring would misstate the randomized contrast.

The distinction between a relative effect and an absolute effect is also relevant. The registry reports a regression-based risk ratio, while an unadjusted recalculation expresses the contrast as a risk difference. Each scale answers a related but different descriptive question. Both are useful when clearly identified, but their estimates should not be conflated.

Finally, the study offers a useful example of the limits of registry-level reporting. The record supplies the design labels, outcome definitions, arm counts, and reported analyses, but not the full statistical plan, missing-data methods, multiplicity approach, or several implementation details. Transparent interpretation means describing what the estimates show while keeping those unanswered methodological questions visible, rather than filling them with assumptions.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific limitations affect interpretation of the registry results. The primary endpoint is narrowly defined as death from any cause within 30 days after index surgery. It does not represent longer-term mortality, nonfatal complications, or all possible consequences of perioperative care. The record does not report cause-specific mortality or more detailed information about the circumstances of deaths.

The standard-of-care arm was monitored, and ACT clinicians could contact operating rooms when clinically necessary for patient safety. This makes the treatment contrast more specific than monitoring versus no monitoring. The registry does not report how often that contact occurred, how often the intervention arm's clinicians provided extra support, or how consistently the two strategies were implemented. Those unreported details limit assessment of treatment separation and fidelity.

The primary-outcome population field is blank, and the record does not describe eligibility criteria in detail. It also does not report the randomization unit, the identity of the masked party, allocation concealment, or the analysis population. The single-masked label alone does not resolve those questions. The reasons for different denominators across outcome measures are also not reported, and neither the missing-data approach nor outcome-specific completeness is described.

The record does not provide the original sample-size justification, a detailed statistical analysis plan, interim-analysis information, or a multiplicity strategy. It lists seven secondary outcome domains, but detailed results are not reported for all of them in the registry record. The adverse-event fields report zero affected participants in each category, but event definitions and ascertainment details are not described. These are limits of the information in the registry record; they should not be treated as evidence that the underlying trial necessarily lacked those procedures or information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Telemedicine Control Tower for the Operating Room: Navigating Information, Care and Safety — NCT03923699.
• Registry record last updated 2024-07-17; status last verified 2024-06.
• Results first posted 2024-07-17.
• 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

NCT03923699 is a completed, Phase 3, randomized, single-masked, parallel pragmatic trial sponsored by Washington University School of Medicine. The registry lists enrollment of 79,560 and compares standard-of-care monitoring with Anesthesia Control Tower monitoring. The primary endpoint is death from any cause within 30 days of index surgery, in or out of hospital.

The sponsor-reported Poisson regression gives a risk ratio of 0.96, with a 95% confidence interval from 0.85 to 1.08 and p = 0.41. An unadjusted recalculation gives a risk difference of -0.001, with a 95% confidence interval from -0.003 to 0.001. Both intervals include their respective no-difference values. The registry does not report the original sample-size justification, detailed missing-data methods, multiplicity strategy, or full statistical analysis plan, limiting interpretation beyond the posted results.