Relative Patient Benefits of a Hospital-PCMH Collaboration Within an ACO to Improve Care Transitions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Relative Patient Benefits of a Hospital-PCMH Collaboration Within an ACO to Improve Care Transitions (NCT02130570), a randomized na study. The primary outcome is Proportion of Participants With an Adverse Event Within 30 Days After Index Discharge Date.

2. Clinical Question

The clinical question is about the post-discharge period and the experience of returning home after hospitalization. The registry’s study description identifies medication issues, worsening medical problems, readmission, recovery of function, and patients’ views of discharge as concerns of interest. The primary endpoint captures whether an adverse event occurred within the stated follow-up window; it does not, by itself, describe the event’s nature, severity, or effect on each participant. The registry record does not report detailed inclusion criteria, the hospitals and practices involved, or the operational definition of every adverse event. Those omissions limit how specifically the population and intervention contrast can be characterized from the record.

3. Trial Design

This was a randomized study with a single masking designation and a sequential model in the registry. The record does not state who was masked, what sequential refers to in operational terms, or whether there were any departures from the assigned treatment. The phase is listed as NA. The study was sponsored by Brigham and Women’s Hospital and is marked completed. The recorded enrollment was 1679.

The two groups were the Multi-Model Intensive Discharge Program and Usual Care. The primary endpoint was the proportion of participants with an adverse event within 30 days after the index discharge date. The primary outcome population description says that 22 enrolled patients were lost to follow-up and therefore excluded from the analysis; examples include withdrawal of consent and death during the index admission. The posted arm sizes for this outcome are 978 for the program and 679 for usual care. The registry does not report additional details about the analysis population, handling of missing outcomes, or whether all randomized participants were analyzed according to assigned group.

The registry lists six outcome measures and five analyses. The secondary outcomes include new or worsening signs or symptoms within 30 days, nonelective readmission within 30 days, change in SF-12v2 functional status from one month before admission to 30 days after discharge, patient engagement and opinions of discharge, and post-discharge health care utilization. Results are posted for some, but not all, of those listed outcomes. The record does not provide the protocol, a detailed statistical analysis plan, the original sample-size justification, interim-analysis plans, or a fuller account of allocation procedures. These design and reporting details are not reported in the registry record and cannot be inferred from the randomized designation alone.

4. Participant Flow and Accounting

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

Before assignment: A total of 141 eligible participants were enrolled to 1 pilot practice at Brigham and Women's Hospital and 1 pilot practice at Massachusetts General Hospital. These participants received the study Intervention so that we could troubleshoot and refine the Intervention procedures. These participants are NOT counted in the final enrollment number.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 1679 participants were enrolled in the study, however, 22 patients were lost to follow-up and therefore not included in the analysis (e.g., patient withdrew consent, patient died during index admission).

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 Proportion of Participants With an Adverse Event Within 30 Days After Index Discharge Date, measured over 30 days after discharge.

The primary endpoint measures the proportion of participants who experienced an adverse event within 30 days after the index discharge date. It is a binary outcome at the participant level: the endpoint concerns whether an event occurred during the stated period, rather than how many events a participant experienced or how severe an event was. The registry names the outcome as a proportion of participants and gives a 95% confidence interval for each arm.

This kind of endpoint is used to summarize the frequency of a specified event in each study group and to compare those frequencies. It is relevant to a discharge-transition study because the period after leaving hospital can include new or worsening health problems, medication issues, and readmission, all of which the study description identifies as concerns. An adverse-event endpoint can capture a broad safety or post-discharge outcome, but the registry record does not give a detailed definition or classification scheme for the primary adverse events. It also does not report the individual event types contributing to the primary endpoint.

The endpoint should therefore be interpreted according to its recorded definition and follow-up window, not as a comprehensive measure of recovery or the overall discharge experience. A participant-level proportion also does not show the timing, recurrence, or severity of events. Those dimensions would require additional outcome details, which are not reported in the registry record.

7. Results Posted in the Registry

• Multi-Model Intensive Discharge Program: 0.2% (2/978) versus 0.3% (2/679) on control; risk difference -0.1 percentage points (95% CI -0.6 to 0.4), risk ratio 0.69 (0.10–4.92); unadjusted two-proportion z-test p = 0.713.

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.

Proportion of Participants With New or Worsening Signs/Symptoms Within 30 Days of Discharge

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Multi-Model Intensive Discharge Program: 0.9% (9/978) versus 0.9% (6/679) on control; risk difference 0.0 percentage points (95% CI -0.9 to 1.0), risk ratio 1.04 (0.37–2.91); unadjusted two-proportion z-test p = 0.938.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Multi-Model Intensive Discharge Program and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients With a Nonelective Readmission Within 30 Days of the Index Discharge Date

• 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:
  • Multi-Model Intensive Discharge Program: 10.9% (107/978) versus 11.5% (78/679) on control; risk difference -0.5 percentage points (95% CI -3.6 to 2.5), risk ratio 0.95 (0.72–1.25); unadjusted two-proportion z-test p = 0.728.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Multi-Model Intensive Discharge Program and the control. The interval gives the range of effects that remain compatible with the data.

Change in Functional Status on the Modified Medical Outcomes Survey Short Form-12 (SF-12v2) From One Month Prior to Admission to 30 Days After Discharge.

• 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:
  • Multi-Model Intensive Discharge Program: mean 47.25 versus 46.14 on control; difference 1.11 (95% CI 0.33 to 1.89), standardized effect d = 0.14; z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Multi-Model Intensive Discharge Program than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary outcomes with posted results, the overall pattern is mixed rather than uniformly favoring one group. The sponsor’s reported analyses indicate statistical evidence for differences in the symptom and functional-status outcomes, while the reported readmission analysis does not. The simple unadjusted recalculations do not reproduce that same pattern across outcomes. These differences are not resolved by the registry record, and the secondary results should be viewed with the primary discrepancy in mind.

The secondary endpoints address distinct aspects of the post-discharge period: symptoms, readmission, functional status, patient engagement and opinions about discharge, and health care utilization. They are not interchangeable measures of a single construct. A result for one does not establish a result for another, nor does a difference on a secondary endpoint necessarily explain the primary outcome. The registry lists five secondary outcomes, but the detailed results available in the record are not complete for every listed outcome; results not posted are not reported in the registry record.

Unadjusted secondary results carry less weight because several outcomes are examined and the registry does not report a multiplicity strategy. As a general statistical principle, testing multiple outcomes creates more opportunities for apparently unusual results by chance. Without a prespecified hierarchy or adjustment plan, isolated p-values should not be treated as confirmatory on their own. The record also does not report the full analysis plan or clarify which secondary analyses were planned in advance. These limitations favor interpreting the secondary results as supporting context rather than as independent confirmation of the primary finding.

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

• Proportion of Participants With New or Worsening Signs/Symptoms Within 30 Days of Discharge
• Number of Patients With a Nonelective Readmission Within 30 Days of the Index Discharge Date
• Change in Functional Status on the Modified Medical Outcomes Survey Short Form-12 (SF-12v2) From One Month Prior to Admission to 30 Days After Discharge.
• Proportion of Participants With Positive Responses Regarding Patient Engagement and Opinions of the Discharge Process
• Post-Discharge Health Care Utilization

9. Statistical Interpretation

10. Statistical Methods Explained

What does randomization contribute?

Random allocation is intended to make the groups comparable, on average, with respect to factors present before assignment. This supports a comparison of outcomes between the assigned groups. Randomization does not guarantee that every characteristic is balanced in a particular study, nor does it resolve missing outcome data, measurement differences, or discrepancies in reported results. The registry identifies the study as randomized but does not report the allocation sequence, concealment procedures, or a full account of how assignment was implemented.

What is a proportion and what is a risk difference?

A proportion describes the share of participants in a group who experienced the outcome. A risk difference compares the two group proportions by expressing the absolute difference on the same scale. A risk difference near zero indicates little separation between the two estimated proportions, while an interval spanning zero leaves uncertainty about the direction of the difference under that calculation. These are general interpretations of the statistics, not additional findings about the trial.

The registry’s recalculated primary risk difference is -0.001, with a 95% confidence interval from -0.006 to 0.004 and p = 0.713. The interval includes zero. But the calculation is based on posted summary counts of 2 and 2, while the arm outcome summaries are 0.18 and 0.23. Since the record flags a discrepancy, this unadjusted calculation should not be treated as a replacement for the sponsor’s own analysis.

What does an incidence rate ratio express?

An incidence rate ratio compares event rates between groups, rather than simply comparing the proportion of participants with at least one event. In general, a ratio below one represents a lower rate in the numerator group relative to the reference group; a confidence interval that excludes one indicates that the data are inconsistent with the null ratio at the corresponding nominal level, under the model used. The sponsor reports an incidence rate ratio of 0.52, a 95% confidence interval from 0.30 to 0.91, and p = 0.02 for the primary outcome. The record labels the method as a regression analysis, but does not explain the rate construction or model details. The reported analysis therefore cannot be fully reproduced from the registry record.

Why do models matter?

Regression methods can account for covariates or model features that are not represented in a simple unadjusted comparison. Logistic regression is commonly used for binary outcomes and estimates odds ratios; linear regression is commonly used for continuous outcomes and estimates mean differences; count or rate regression can estimate incidence rate ratios. These are general descriptions. The registry lists a logistic regression analysis for readmission, a linear regression analysis for functional status, and a regression analysis for the primary outcome and symptoms. The exact covariates, link functions, assumptions, and model diagnostics are not reported in the registry record.

The posted recalculations are described as simple, unadjusted comparisons based on summary statistics. An unadjusted comparison does not necessarily target the same estimand as a regression analysis. Differences can arise from model adjustment, outcome definitions, analysis populations, or other analytic choices. The record does not identify which of these explains the observed disagreement, so it is not possible to attribute the differences to any particular method.

Why can over-dispersion matter?

As a general statistical point, count and rate models often rely on assumptions about how event counts vary around their expected values. Over-dispersion means the observed variability is greater than the model’s basic assumptions allow. If it is not accounted for, estimated uncertainty can be too small, which can make confidence intervals too narrow and p-values too optimistic. The registry does not report a diagnostic for over-dispersion or explain whether this issue was assessed. It is therefore a general consideration, not a claim that over-dispersion affected this study.

What do p-values and confidence intervals tell the reader?

A p-value summarizes how compatible the observed data are with a specified null model, assuming the analysis model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A confidence interval gives a range of estimates compatible with the data and method at its stated confidence level. A wide interval indicates less precision than a narrow interval, though the practical meaning also depends on the outcome scale. For this study, the reported sponsor and recalculated statistics should be kept distinct because they disagree for the primary outcome and some secondary outcomes.

What should be considered when comparing the analyses?

Interpretation requires identifying the group order, outcome scale, analysis population, and method for each estimate. The registry labels Usual Care as the control group and posts the program-versus-usual-care comparisons. A difference, ratio, and odds ratio have different null values and different interpretations. A risk difference is centered on zero under the null, whereas a ratio is centered on one. The fact that the endpoints or groups are similarly named does not make estimates from different methods interchangeable. The posted comparisons should be read with their stated metric and interval, and the sponsor’s reported model result should not be silently substituted with a recalculation.

The registry’s primary analysis discrepancy is material because the displayed group proportions, posted counts, and reported model result do not tell a single coherent numerical story. For that reason, the sponsor analysis takes precedence over the simple recalculation, while the discrepancy remains a limitation of the available record. More complete reporting of the analysis plan and outcome data would be needed to independently verify the reported result.

11. Confidence Intervals and Precision

A confidence interval describes uncertainty around an estimate under the analysis method used. It is not a guarantee that the true effect lies in the interval, and it does not represent the range of individual participant outcomes. A narrower interval generally indicates greater statistical precision than a wider interval on the same scale. Whether an interval is clinically important depends on the outcome and the range of effects that matter, information not reported in the registry record.

For the primary outcome, the arm-level 95% confidence intervals are 0.15 to 0.21 for the Multi-Model Intensive Discharge Program and 0.2 to 0.27 for Usual Care. The unadjusted recalculated risk-difference interval is -0.006 to 0.004, which includes zero. The sponsor-reported incidence rate ratio interval is 0.30 to 0.91, which excludes one. These intervals concern different statistics and arise from analyses that conflict with the posted summary counts. Their apparent precision cannot resolve the underlying inconsistency; the registry does not explain how the figures relate to one another.

Precision also varies across secondary outcomes. The recalculated intervals for symptoms and readmission include the null values for their respective measures, while the functional-status interval of 0.326 to 1.894 does not include zero. The sponsor’s reported results differ from some of those recalculated comparisons. An interval’s width should be read in the units of its estimate, not compared directly across different outcome scales. In addition, the registry does not provide confidence intervals for the sponsor’s functional-status estimate.

All confidence intervals describe sampling uncertainty under the methods used; they do not account automatically for missing data, outcome measurement error, model misspecification, or selective reporting. Those concerns require information beyond the interval itself. In this record, the discrepancy between analyses and the absence of some analysis details make that distinction especially important.

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 express participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The stated 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. These are planning illustrations computed from observed effects, not the trial’s original design assumptions, which 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 to have an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions were correct. The 90% power column makes the same kind of illustration for a 90% chance. Higher target power generally requires more participants under otherwise unchanged assumptions. The rows planning for 100%, 75%, and 50% of the observed effect show the consequence of targeting progressively smaller effects: smaller effects need more participants to distinguish them from random variation.

These values should not be read as a retrospective measure of how likely this completed trial was to produce a statistically significant result. They are not observed power. They are conditional planning illustrations and inherit the uncertainties of the observed effect used to generate them. The primary discrepancy is an additional reason to interpret planning figures based on the observed effect cautiously. For outcomes expressed as counts or continuous measures, the relevant scale and assumptions differ, so the figures should be considered for their own endpoint rather than compared as if they were interchangeable. The original rationale for the trial’s enrollment and its planned power are not reported in the registry record.

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 = 0.003; treatment proportion p₁ = 0.002; average p̄ = 0.002.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.0706 = 0.1383.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.0706 = 0.0594.
4. n = (0.1383 + 0.0594)² / (-0.0009)² = 48,180.4, rounded up to 48,181 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 <- 0.00294550810014728                          # control proportion
p1 <- 0.00204498977505112                          # 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(2130570)
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 = 48,181 (80% power), 64,500 (90% power)
 75% of observed effect: n per arm = 89,510 (80% power), 119,827 (90% power)
 50% of observed effect: n per arm = 210,067 (80% power), 281,219 (90% power)
power.prop.test: 48180.4 
Simulated power at n = 48,181 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 reported primary analysis gives an incidence rate ratio of 0.52, a 95% confidence interval from 0.30 to 0.91, and p = 0.02. The simple unadjusted recalculation from the posted comparison counts instead gives a risk difference of -0.001, a 95% confidence interval from -0.006 to 0.004, and p = 0.713. The arm summaries show proportions of 0.18 and 0.23, while the comparison counts are 2 and 2. The registry identifies a discrepancy among these entries but does not explain it.

Because the discrepancy is flagged, the sponsor’s own analysis takes precedence over the simple recalculation. That does not make the record internally consistent or independently verifiable; it means the sponsor analysis is the appropriate reported result to quote rather than treating the unadjusted recalculation as the trial’s result. The sponsor analysis is described as regression, but the detailed model specification, data used, and reason for the differences are not reported in the registry record.

A similar distinction applies to the secondary outcomes. Sponsor-reported analyses and simple recalculations do not always agree, including for functional status. Each statistic should therefore be attributed to its analysis rather than combined into a single estimate. The registry record does not provide enough detail to determine whether model adjustment, analysis populations, outcome definitions, or other factors account for the disagreements.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple outcomes and analyses, but does not report whether the statistical plan controlled the overall chance of false-positive findings across them. Multiplicity refers to the consequences of conducting multiple statistical tests: even when each test is interpreted at its nominal level, the chance of at least one apparently positive result across a family of tests can increase. This is a general statistical concern, not evidence that any specific result in this study is false.

The record does not describe a multiplicity adjustment, testing hierarchy, primary-secondary gatekeeping procedure, or designation of particular secondary analyses as confirmatory or exploratory. Consequently, the reported secondary p-values should not be interpreted as if they necessarily had a study-wide error rate controlled. The original statistical analysis plan is not reported in the registry record, so it is not possible to assess whether the posted analyses reflect prespecified choices.

Missing data are also relevant. The primary outcome description says that 22 patients were lost to follow-up and excluded from that analysis, with examples including withdrawal of consent and death during the index admission. The record does not report whether missing outcomes differed between groups, how missingness was assessed, or whether sensitivity analyses were performed. It also does not explain whether the stated exclusions were applied to every outcome or only to the primary analysis population. Excluding participants with unavailable outcomes can affect an estimate if the missingness is related to outcome status or group assignment; this is a general possibility, not a claim about this study.

The registry does not report the full analysis populations for the secondary endpoints, an intention-to-treat statement, imputation procedures, or other missing-data methods. It is therefore not possible to determine from this record whether the reported analyses preserve the benefits of randomization or how robust the estimates are to missingness. The primary population description provides some information, but it is not a complete account of participant flow or outcome availability.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The posted serious adverse event figures list 0 serious adverse events among 978 participants at risk in the Multi-Model Intensive Discharge Program group and 0 among 679 participants at risk in the Usual Care group. The record also lists 0 other adverse events in each group. No serious adverse event terms are listed. These entries describe the safety data as posted; they do not establish that no adverse events of any kind occurred, since the registry’s event categories and reporting completeness are not further explained.

The deaths fields are empty rather than populated with a count, so deaths are not reported in the registry record. The primary endpoint is a separate outcome measuring the proportion with an adverse event within 30 days after discharge. Its posted proportions and the safety figures should not be assumed to describe the same event definition, period, or analysis. The record does not explain how these safety entries relate to the primary endpoint, nor does it provide event-level details. Zero counts in the posted categories should therefore be read narrowly as the figures recorded in those fields, not as a complete characterization of all possible harms.

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

The study record describes a randomized comparison of a multi-model discharge program with usual care and reports a primary adverse-event outcome within 30 days after discharge. The sponsor’s analysis reports an incidence rate ratio of 0.52 with a 95% confidence interval from 0.30 to 0.91 and p = 0.02. That is the sponsor’s reported statistical result, and it takes precedence over the conflicting unadjusted recalculation. The registry also shows arm proportions and event counts that do not align with that recalculation or with one another. The result therefore needs to be interpreted alongside an unresolved reporting discrepancy.

The estimate does not, on its own, establish the size or practical importance of any difference for patients. The registry does not provide a sufficiently detailed definition of the primary adverse events, the full analysis model, or the explanation for the inconsistency in the reported values. Nor does a primary outcome answer every question about symptoms, readmission, function, engagement, or care utilization. Those outcomes are distinct, and their posted analyses are mixed and not fully consistent with the recalculations.

The record also does not provide the original sample-size justification, a complete missing-data approach, or a multiplicity plan. These limitations matter when judging how reliable and confirmatory the findings are. Results from this trial should be understood as estimates reported for the study groups and follow-up period recorded, with uncertainty about some analytic details. They do not establish that the program will have the same results in other hospitals, practices, or patient groups. The registry’s own stated objective included understanding implementation across settings and which patients might benefit most, but those conclusions are not reported in the results available in this record.

18. Why This Trial Matters Statistically

This trial is statistically instructive because the record places several forms of evidence side by side: arm-level outcome summaries, a sponsor-reported regression analysis, and an unadjusted recalculation from posted summary counts. These should not be conflated. They use different statistical measures, and in this case they do not agree. Recognizing that distinction is essential: a recalculation is a check based on summary data, not a substitute for the sponsor’s analysis when the registry marks a discrepancy.

The study also illustrates why effect estimates need to be read with their uncertainty and analysis scale. A proportion, risk difference, incidence rate ratio, odds ratio, and mean difference answer related but nonidentical questions. The null value and interpretation depend on the measure. Confidence intervals convey sampling uncertainty but cannot repair inconsistencies in the underlying reported data or compensate for unavailable model details.

Several secondary outcomes extend the question beyond a single event indicator to symptoms, readmission, function, patient experience, and utilization. That breadth is clinically relevant to a discharge-transition study, but multiple outcomes also raise a multiplicity concern when no adjustment or hierarchy is reported. Statistical interpretation therefore depends not only on whether individual p-values are small, but also on which analyses were planned, how missing outcomes were handled, and how consistent the different measures are. Those details are not reported in the registry record.

The case highlights the importance of transparent registration and complete results reporting. Clear definitions, participant flow, model specifications, and reconciliation of counts with estimates would make the findings easier to interpret and verify. The trial’s randomized design is useful context, but design labels alone do not answer those reporting questions.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations specific to this record constrain interpretation. The primary outcome is described as an adverse event within 30 days after the index discharge date, but the event definition and classification are not detailed. The arm-level proportions, posted comparison counts, and sponsor analysis are inconsistent, and the registry does not explain the discrepancy. The sponsor’s own analysis takes precedence over the simple recalculation, but the available record does not permit independent reconciliation of the figures.

The primary population description reports loss to follow-up and exclusion of 22 patients, but does not provide a full participant flow or describe missing-data methods. It is not clear whether the same population definition applies to all outcomes. The record also does not report the original sample-size justification, statistical analysis plan, interim analyses, adjustment covariates, model diagnostics, or multiplicity procedures. These are omissions in the registry record, not evidence that such procedures were or were not used.

Some secondary results have additional limitations. Sponsor analyses and simple recalculations differ for some outcomes, and detailed results are not posted for every listed secondary measure. The symptoms arm summary includes an upper confidence limit of 1.01 for a proportion, and the record does not explain this value. It should not be silently altered or treated as evidence of a particular correction. The registry also gives no detailed information about implementation across hospitals and practices or variation in treatment effects across patient types, despite naming those as study objectives.

Finally, the masking designation is single, but the identity of the masked party is not reported. The meaning of the sequential model designation is not explained. These missing design details, along with outcome and analysis reporting gaps, limit assessment of bias and reproducibility from the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Relative Patient Benefits of a Hospital-PCMH Collaboration Within an ACO to Improve Care Transitions — NCT02130570.
• Registry record last updated 2019-08-20; status last verified 2019-08.
• Results first posted 2019-08-20.
• 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

NCT02130570 is a completed randomized study sponsored by Brigham and Women’s Hospital, comparing the Multi-Model Intensive Discharge Program with Usual Care. The registry records enrollment of 1679 and identifies a primary outcome of adverse events within 30 days after the index discharge date.

The sponsor-reported primary analysis is an incidence rate ratio of 0.52, with a 95% confidence interval from 0.30 to 0.91 and p = 0.02. A discrepancy is flagged between that analysis and the simple recalculation from posted summary counts; the sponsor’s analysis takes precedence. Secondary outcomes cover symptoms, readmission, functional status, patient engagement and discharge opinions, and health care utilization, with mixed results and incomplete reporting across the listed outcomes.

The registry record does not report the original sample-size rationale, full statistical plan, missing-data methods, multiplicity strategy, or enough detail to resolve the primary numerical discrepancy. Those gaps should remain part of any interpretation of the posted findings.