Reducing Veterans Hospitalizations From Community Living Centers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Reducing Veterans Hospitalizations From Community Living Centers (NCT04195880), a randomized na study. The primary outcome is Hospital Admissions Per Person Year Alive Measured at the Facility Month Level.

2. Clinical Question

3. Trial Design

NCT04195880, titled “Reducing Veterans Hospitalizations From Community Living Centers,” is listed as a completed, randomized, parallel study. The intervention was implemented and evaluated in VA CLCs. The registry records enrollment of 6543 participants and identifies the sponsor as the VA Office of Research and Development. The study is classified as quality improvement, and its phase is listed as not applicable. Masking is recorded as none, so the trial is open-label as described in the registry.

The comparison involved eight experimental VA CLCs and eight control CLCs. The experimental facilities received INTERACT. Control facilities were matched to experimental facilities on size, location to a VA Medical Center, and hospitalization rates; they continued care as usual without the intervention. The record calls the allocation randomized, but does not describe the unit or sequence of randomization, allocation concealment, or how randomization was combined with facility matching. Those design details are not reported in the registry record.

The primary outcome covers 36 months: 18 months of active study and 18 months preceding introduction of the intervention in the experimental facilities. It was constructed from electronic medical record data for each facility and month. The registry lists hospital admissions per person year alive as the outcome unit. The intervention’s stated goal was to improve care following acute changes in condition while reducing hospitalization rates; that statement describes the project’s aim, not a conclusion about its effect.

The record does not report the original sample-size justification, the planned statistical analysis in sufficient detail, or whether interim analyses were planned or conducted. It also does not describe participant flow, exclusions, adherence to the assigned intervention, or missing outcome data. Enrollment and the group counts are recorded, but those entries alone do not establish how every participant contributed to each outcome analysis.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Hospital Admissions Per Person Year Alive Measured at the Facility Month Level, measured over 36 months.

The primary endpoint is hospital admissions per person year alive, calculated at the facility-month level. It represents the rate of hospital admissions relative to the amount of time people were alive and at risk of hospitalization. A rate accounts for differing amounts of time at risk, unlike a simple count of admissions. The registry states that the measure was constructed from electronic medical record data and was not derived from a scale.

The outcome description covers each of the 16 facilities per month during the 18 months of active study and the 18 months preceding introduction of INTERACT in experimental facilities. The listed timeframe is 36 months. The arm summaries report means of 5.5 for experimental facilities and 5.8 for controls, with a standard error of 2.5 for each. The comparison is expressed as a rate ratio, which relates the experimental group’s rate to the control group’s rate. A value below 1 indicates a lower estimated rate in the experimental group; it does not by itself establish why the rates differed.

Using a rate is relevant because exposure time can differ among people, and the measure is intended to describe admissions in relation to time alive and at risk. However, the registry does not fully explain the construction of person-time, the handling of repeated admissions, or how facility-level data were incorporated into the reported analysis. These details are not reported in the registry record.

7. Results Posted in the Registry

• Experimental VA Community Living Centers: 5.50 versus 5.80 (hospitalizations per person year alive) on control; rate ratio 0.95 (95% CI 0.94–0.96, approximate, Poisson model); p ≈ <0.001.

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.

Potentially Avoidable Hospitalizations

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Experimental VA Community Living Centers: 0.30 versus 0.20 (hospitalizations per person year alive) on control; rate ratio 1.50 (95% CI 1.38–1.63, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for Experimental VA Community Living Centers than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome, potentially avoidable hospitalizations. The unadjusted comparison points in a different direction from the primary outcome comparison: the secondary rate is estimated higher in experimental facilities relative to controls, while the primary rate-ratio estimate is lower. This difference means the primary outcome alone does not describe every hospitalization-related measure recorded in the study. The secondary result should be interpreted as a distinct outcome, not as a direct contradiction, because the registry does not fully define how potentially avoidable admissions were classified or how the two measures relate.

No sponsor analysis is posted for the secondary outcome. Its comparison is therefore an unadjusted recalculation rather than a reported result from the sponsor’s negative-binomial model. The registry does not state that the secondary analysis was prespecified, how it was prioritized, or whether a multiplicity procedure was used. The number of posted outcome measures is two, but the record does not give a comprehensive analysis plan covering all outcomes or analyses that may have been considered.

When multiple outcomes are examined, the chance of obtaining a nominally unusual result somewhere among them can increase. Adjustment procedures or a prespecified hierarchy can help control how evidence is interpreted across several comparisons. Without a reported plan, unadjusted secondary p-values carry less weight than a single prespecified primary comparison and are best treated as exploratory. They can identify patterns that deserve attention, but should not be treated as independent confirmation of the primary finding.

The contrasting directions also underscore the importance of endpoint definitions. The registry does not report the criteria for potentially avoidable hospitalization, the adjudication process, or whether coding and classification were consistent across facilities. It does not provide a sponsor model estimate for this endpoint. The secondary data add context to the outcome profile, but the available record does not support a detailed assessment of its clinical or statistical relationship to the primary measure.

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

• Potentially Avoidable Hospitalizations

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is an event rate: hospital admissions relative to person time alive and at risk of hospitalization. Rate methods are useful when the amount of time at risk differs across people or groups. A rate ratio compares the rate in one group with the rate in another. In this analysis, the comparison is experimental facilities relative to control facilities. A rate ratio of 1 corresponds to equal rates; a ratio below 1 corresponds to a lower estimated rate in the experimental group, and a ratio above 1 corresponds to a higher estimated rate.

What does the posted rate ratio represent?

The posted primary rate ratio is 0.948. The associated interval runs from 0.937 to 0.960. The recalculation is based on posted event and exposure summaries, using a Poisson approach, and is unadjusted. It does not have the same model specification as the sponsor’s reported negative-binomial regression. The p-value for this unadjusted comparison is <0.001. An unadjusted result does not account for covariates or design features unless they are built into the calculation; the registry does not report such adjustments for this recalculation.

The arm-level primary summaries are means with standard errors. A standard error describes the estimated sampling uncertainty in a summary statistic, rather than the spread of individual observations. The reported standard error is 2.5 in each arm. It should not be read as an estimate of the range of facility outcomes or participant-level outcomes. The registry does not provide the facility-specific outcome values, so variability across facilities cannot be inspected from the posted summaries.

Why distinguish Poisson and negative-binomial models?

Poisson regression is a common model for event counts, usually with exposure time incorporated so that rates can be compared. A basic Poisson model assumes that the conditional variance of counts is related to the conditional mean. If the observed counts vary more than that assumption allows, the data are over-dispersed. Negative-binomial regression is a common alternative that allows additional variation beyond the basic Poisson structure. This general distinction matters because a model that represents variability poorly can produce uncertainty estimates that are too narrow or too wide.

The registry identifies the sponsor’s method as a negative-binomial regression coefficient, but does not post the coefficient, confidence limits, model formula, or diagnostics. It is therefore not possible to determine from the record how the sponsor modeled exposure, facility clustering, matching, or time. The recalculation uses a Poisson method and is not a substitute for the sponsor’s specified model. The registry’s reported sponsor p-value is <.05, while the coefficient’s magnitude and direction are not numerically available.

What does a confidence interval convey?

A confidence interval describes the range of estimates compatible with a statistical procedure and its assumptions. In repeated use of the same procedure under those assumptions, intervals would vary from sample to sample; the confidence level refers to the long-run coverage property of that procedure. It is not a guarantee that the true effect lies within a particular interval, and it does not capture every source of uncertainty. For the primary recalculation, the interval is 0.937 to 0.960. Its endpoints are close to the point estimate, indicating relatively limited statistical uncertainty under the calculation’s assumptions. That precision does not address possible systematic bias or model misspecification.

The posted primary comparison identifies its interval as not based on the arm-level confidence limits. It is a recalculated comparison, not a confidence interval reported alongside the sponsor’s coefficient. The sponsor’s own estimate and interval are not reported in the registry record. Consequently, the posted interval should be interpreted with the method that generated it, not treated as a direct presentation of the sponsor’s regression result.

How should p-values be interpreted?

A p-value measures how incompatible the observed data, or more extreme data, are with a specified null model under the analysis assumptions. It is not the probability that the null hypothesis is true, nor the probability that the result occurred “by chance.” The primary recalculation’s p-value is <0.001. The sponsor’s negative-binomial analysis reports p <.05. These values are associated with different analyses and should not be treated as interchangeable measures of the same estimate. Neither p-value alone conveys the size, importance, or causal certainty of an effect.

Because outcomes are clustered by facility and measured over time, observations within a facility may be related. General statistical methods for clustered or repeated data account for such dependence in the variance calculation or model structure. The record does not report enough detail to establish how this dependence was handled in the sponsor analysis. Likewise, the facility matching characteristics are described, but the registry does not report whether matching was incorporated in the statistical model. These omissions limit independent assessment of the reported inferential results.

11. Confidence Intervals and Precision

The primary recalculated rate ratio is 0.948, with a confidence interval from 0.937 to 0.960. The interval lies below 1, which is consistent with a lower estimated admission rate in experimental facilities than in controls under the unadjusted Poisson calculation. Its relatively narrow span indicates that the calculation produces a precise estimate on that model’s terms. Precision is not the same as validity: a narrow interval does not account for unmodeled facility clustering, systematic differences, or errors in outcome measurement.

The arm summaries report a standard error of 2.5 for each mean. Standard errors reflect uncertainty in estimated means, not the range of outcomes across participants or facilities. The registry does not provide a confidence interval for the sponsor’s negative-binomial coefficient, nor does it provide the coefficient itself. The sponsor’s estimate therefore cannot be assessed for magnitude or precision from the posted analysis entry.

The interval for the primary recalculation is distinct from a sponsor-reported interval. It is based on the recalculated comparison, and its interpretation depends on the assumptions of that method. The registry does not report model diagnostics, adjusted estimates, or sensitivity analyses that would show whether the interval remains similar under other reasonable approaches. Nor does it describe how facility-level dependence was handled in the sponsor’s model.

Accordingly, the interval communicates statistical precision conditional on the recalculation’s assumptions, not certainty about a causal effect or transportability to other facilities. The primary estimate should be read together with the study’s limited number of facilities, the facility-level nature of the outcome, and the incomplete reporting of the sponsor’s model results.

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, not total event counts. This is not a time-to-event calculation. The accompanying curve represents the same planning relationship visually: the number of participants needed rises as the effect targeted for detection becomes smaller. For the full observed effect, the illustration gives 329 participants per arm for 80% power and 440 participants per arm for 90% power. For planning for 75% of the observed effect, the corresponding figures are 581 and 777 participants per arm. For planning for 50% of the observed effect, they are 1,297 and 1,736 participants per arm.

In plain language, 80% power means that, if the specified effect and planning assumptions were correct, the design would have an 80% chance of detecting that effect at the stated significance threshold. The 90% power column describes a higher target chance of detection under the same conditions, which generally requires a larger planned sample. These are hypothetical planning quantities, not observed power and not a report of the trial’s original design calculations.

The registry’s planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It sets the effect to detect as a stated fraction of the observed effect. These assumptions describe the posted illustration; the original trial design assumptions and sample-size justification are not reported in the registry record. Because the endpoint is an event rate and the trial compares facilities, these individual-level participant figures should not be read as a complete design recommendation that accounts for all possible clustering or implementation considerations.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 5.8000; treatment rate λ₁ = 5.5000 events per patient-year; follow-up T = 3.00 years.
2. n = (1.96 + 0.842)² × (1/5.8000 + 1/5.5000) / (3.00 × [ln(0.948)]²) = 328.6, rounded up to 329 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
lambda0 <- 5.8                      # control rate, events per patient-year
lambda1 <- 5.5                      # treatment rate
tt      <- 3                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(4195880)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 329 (80% power), 440 (90% power)
 75% of observed effect: n per arm = 581 (80% power), 777 (90% power)
 50% of observed effect: n per arm = 1,297 (80% power), 1,736 (90% power)
Simulated power, Poisson counts, n = 329 per arm: 0.800
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.629

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor’s own primary analysis is identified as a negative-binomial regression coefficient and is classified as a superiority analysis. The registry reports p <.05, but does not provide the coefficient estimate or its confidence limits. Without those values, the sponsor’s result cannot be used to quantify the estimated difference or evaluate its precision directly.

The posted rate ratio of 0.948 and confidence interval from 0.937 to 0.960 are an unadjusted recalculation using a Poisson approach. They are not the sponsor’s negative-binomial coefficient or interval. The recalculation indicates a lower estimated primary rate in the experimental group under its own assumptions, but differences between model specifications mean its numerical result should not be presented as if it were the sponsor’s result.

The registry does not report the negative-binomial model formula, adjustment variables, handling of facility-level dependence, or diagnostic checks. The two analyses therefore offer different levels of detail: the recalculation supplies an estimate and interval from posted summaries, while the sponsor entry supplies a method label and significance statement without the underlying estimate. Interpretation of the sponsor’s analysis remains limited by that missing information.

15. Multiplicity, Missing Data and Analysis Populations

The registry posts a primary outcome and one secondary outcome, and identifies one reported analysis for the primary outcome. It does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a plan for interpreting secondary analyses alongside the primary analysis. The absence of this information does not establish that no such plan existed; it means the plan is not reported in the registry record. Without it, unadjusted secondary results warrant more cautious interpretation because multiple comparisons can increase the chance of at least one apparently notable result.

Missing-data methods are not described. The record does not report the amount or pattern of missing outcome data, how incomplete facility-month observations were handled, or whether any imputation or exclusion procedure was used. It also does not report whether exposure time was complete for all participants or how person-time was assembled. These details matter for rate outcomes because both event counts and time at risk contribute to the estimate.

The analysis population is not fully specified. Enrollment is recorded as 6543, and group counts are listed, but the registry does not describe inclusion and exclusion rules for the primary analysis, participant flow, or whether all enrolled participants were included in each outcome calculation. The record also does not say whether analysis followed assignment regardless of intervention uptake, or whether any per-protocol or other population was used.

The trial is labeled randomized, but details of randomization and its implementation are not reported. The facility-level nature of intervention delivery raises questions about how correlation within facilities and the matching structure were represented in the analysis. The sponsor method is named as negative-binomial regression, but model specification and diagnostics are absent. These reporting gaps limit assessment of potential bias, the adequacy of uncertainty estimates, and the relationship between the sponsor analysis and the unadjusted recalculation.

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 registry’s adverse-event entries show zero serious adverse events, zero other adverse events, and zero deaths in both groups. The at-risk counts are 3205 for experimental facilities and 3338 for control facilities. No serious adverse-event terms are listed. These entries describe what is recorded in the registry, rather than establishing that no adverse events occurred in any broader sense.

The record does not explain the adverse-event definitions, collection procedures, reporting period, or whether event ascertainment was systematic across facilities. It also does not provide details on how events were attributed or whether all participants were followed for safety in the same way. With those details absent, zero recorded events should be read as a registry reporting result, not as evidence that the intervention or usual care had no risks. The trial’s stated primary focus was hospitalization rates, and the posted safety information does not replace a full account of event monitoring.

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

The posted primary recalculation indicates a lower estimated hospital-admission rate in the experimental facilities than in the control facilities. Its rate ratio is 0.948, and its confidence interval is 0.937 to 0.960. This is a statistical comparison based on the available summaries and the recalculation’s assumptions. The sponsor’s own analysis reports a negative-binomial regression result with p <.05, but its coefficient and confidence limits are not posted. The two results should not be conflated.

The findings do not by themselves establish that INTERACT caused the observed rate difference. The record does not give enough information about the randomization process, analysis model, facility-level dependence, missing outcome data, or implementation to resolve all potential sources of uncertainty. The study involved eight experimental and eight control facilities; the participant enrollment count does not remove the importance of the number and structure of facilities when interpreting a facility-based intervention.

The primary outcome is hospital admissions per person year alive, while the secondary outcome is potentially avoidable hospitalizations. Those measures capture related but distinct aspects of hospitalization. The secondary recalculation points in a different direction, and its result is unadjusted with no sponsor analysis posted. The registry does not report a multiplicity plan or enough endpoint-definition detail to explain the contrast. Thus, the primary comparison is not a complete summary of all the hospitalization-related information.

The estimates also do not establish what would happen in other health systems, facilities, or populations. The record describes VA CLCs and does not report the characteristics needed to judge how comparable other settings might be. The project’s stated goals are to improve care during acute changes in condition and reduce hospitalization rates; those goals should be distinguished from the evidence summarized by the posted comparisons. Statistical significance alone does not determine the practical importance of a result.

18. Why This Trial Matters Statistically

This trial is statistically notable because it evaluates an intervention delivered through facilities while the primary outcome is a rate measured over repeated facility-month observations. That structure makes the distinction between participant enrollment and the number of facilities important. The record lists 6543 participants but describes 16 facilities, with eight assigned to each group. Analyses of such data need to account appropriately for how observations within facilities may be related; the registry does not provide enough detail to assess how the sponsor model handled that issue.

The posted results also illustrate why the method and estimate should be considered together. The sponsor’s analysis is identified as negative-binomial regression, while the rate-ratio recalculation uses a Poisson approach and is unadjusted. The recalculation provides an estimate and confidence interval, but does not reproduce the sponsor’s model. The sponsor result, in turn, is missing its coefficient and confidence limits. Clear reporting of both model specifications and estimates would make it easier to assess how closely the findings agree.

Finally, the primary and secondary outcomes do not point in the same direction. This makes transparent outcome definitions, a stated multiplicity strategy, and complete reporting of analysis decisions especially useful. The registry record contains information that supports a focused description of the primary comparison, but leaves important aspects of design and analysis unspecified. Statistically, the lesson is to distinguish an estimated association from a causal conclusion and nominal significance from a complete evaluation of robustness.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

Several limitations specific to this record constrain interpretation. The intervention was delivered at CLCs, and the primary outcome was calculated at the facility-month level, but the registry does not report the model specification used to account for repeated observations or facility-level clustering. It also does not say whether the matching of control facilities on size, location to a VA Medical Center, and hospitalization rates was incorporated into the sponsor’s analysis. The validity of uncertainty estimates cannot be independently assessed without those details.

The sponsor’s negative-binomial analysis is reported without its coefficient estimate or confidence limits. As a result, its effect size and precision are unavailable, and the sponsor result cannot be directly compared with the Poisson-based unadjusted recalculation. The recalculation does not adjust for covariates or provide a sensitivity analysis, and it should not be regarded as a replacement for the sponsor analysis.

The outcome description gives the rate unit and observation period but does not fully explain person-time construction, handling of recurrent admissions, or the operational definition of potentially avoidable hospitalization. The record does not report missing-data procedures, participant-level analysis populations, exclusions, or facility-specific results. It also does not describe intervention fidelity or whether implementation varied among the experimental CLCs.

Finally, only one secondary outcome is posted, with no sponsor analysis and no multiplicity plan reported. Adverse-event entries show no recorded events, but collection and ascertainment details are absent. These are limitations of the information in the registry record; they do not establish that the corresponding methods or information were absent from all study documents.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Reducing Veterans Hospitalizations From Community Living Centers — NCT04195880.
• Registry record last updated 2023-07-27; status last verified 2023-07.
• Results first posted 2020-05-11.
• 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

NCT04195880 is a completed, randomized, parallel evaluation of INTERACT in VA Community Living Centers. The registry records no masking, enrollment of 6543 participants, and eight experimental and eight matched control facilities. The primary outcome is hospital admissions per person year alive, calculated monthly at the facility level across 36 months, including 18 months before and 18 months during active study.

The sponsor’s primary analysis is identified as negative-binomial regression and reports p <.05, but its coefficient and confidence limits are not posted. An unadjusted Poisson recalculation gives a rate ratio of 0.948, with a confidence interval from 0.937 to 0.960 and p <0.001. The secondary outcome is potentially avoidable hospitalizations; its recalculation points in the opposite direction from the primary comparison, and no sponsor analysis is posted for it.

The registry does not report the original sample-size justification, detailed analysis plan, missing-data methods, multiplicity strategy, or enough model detail to assess facility-level dependence. The results therefore describe the posted comparisons, with important design and analysis uncertainties remaining.