Implementing Shared Decision Making (SDM) For Individualized CV Prevention (SDM4IP): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Implementing Shared Decision Making (SDM) For Individualized CV Prevention (SDM4IP) (NCT04450914), a randomized na study. The primary outcome is Reach (RE-AIM): The Percentage of Clinicians Who Ever Used CV Prevention Choice.

2. Clinical Question

The study addressed implementation of shared decision making for individualized cardiovascular prevention in three health systems. Its stated rationale is that preventive care may not be well matched to cardiovascular risk, and that shared decision making could help address this mismatch. The registry identifies the primary outcome as reach, rather than a patient health outcome: it measures clinician use of the tool among clinicians eligible for assessment in each period.

The posted primary results compare reach during active implementation and maintenance with usual care. A secondary outcome concerns whether the predicted marginal probability of statin use is concordant with estimated cardiovascular risk. The available results described in the registry record do not include estimates for that secondary outcome, so the primary interpretation is limited to clinician tool use.

3. Trial Design

The registry describes NCT04450914 as a randomized crossover study of behavioral interventions. It lists CV Prevention Choice Tool and Implementation Facilitation Strategies as interventions. The study is marked completed, with enrollment recorded as 112127. Its primary completion date is 2024-12-31. The registry lists the phase as NA.

Clinicians were organized into three sequences. Sequence 1 began usual care on 9/24/2021 and entered active implementation on 3/24/2022. Sequence 2 began usual care on 4/13/2022 and entered active implementation on 10/14/2022. Sequence 3 began usual care on 6/13/2022 and entered active implementation on 12/13/2022. All three sequences entered the maintenance period on 4/1/2024. In usual care, clinicians had access to the tool in their electronic health record, with no other active implementation described.

The primary outcome is reported for usual care, active implementation, and maintenance. The registry’s primary-outcome population consists of clinicians with at least one eligible clinical encounter during the step being evaluated; those without an eligible encounter during that step were excluded. The arm counts in the primary results therefore describe clinicians in those period-specific outcome groups. The record does not explain how the enrollment figure relates to these clinician counts.

The registry does not report further detail about how randomization was carried out, the allocation process, or the statistical plan specified before the study. It also does not describe the implementation facilitation strategies in enough detail to characterize their individual components. Those design and intervention details are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: This study uses a stepped wedge cluster randomized design. Participants and clinicians could enter the study during any period, and participants and clinicians could be enrolled for more than one period over the course of the study. They are included in each period in which they had an eligible encounter.

Step 1 (Q2/Year 2 through Q1/Year 3)

Step 2 (Q4/Year 2 through Q4/Year 4)

Step 3 (Q4/Year 4 through Q3/Year 5)

Analysis population for the primary outcome, as defined in the registry: Clinicians who had at least one eligible clinical encounter were included in the overall number of participants analyzed for that step. Excluded were clinicians who did not have an eligible encounter during that step.

5. Baseline Characteristics

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

Population: Baseline demographic characteristics are reported for participants at the time of their initial enrollment, and participants were only included once. Baseline demographics were not collected for clinicians.

6. Primary Endpoint

The registry lists the primary outcome as Reach (RE-AIM): The Percentage of Clinicians Who Ever Used CV Prevention Choice, measured over Approximately 3.5 years.

The primary endpoint is reach under the RE-AIM framework: the percentage of eligible clinicians who ever used CV Prevention Choice during the period assessed. Use was recorded in the electronic health record. Eligibility required at least one eligible clinical encounter during the relevant step; clinicians without such an encounter were excluded from that step’s population.

This endpoint addresses whether an intervention is being taken up in routine practice, rather than whether it changes cardiovascular events or patient health. It is useful for assessing implementation because a tool cannot influence care through clinician use if eligible clinicians do not use it. However, reach alone does not establish how often the tool was used, whether its use changed clinical decisions, or whether decisions were better aligned with individual risk.

The posted outcome groups report 40 of 137 clinicians in usual care, 87 of 165 in active implementation, and 54 of 129 in maintenance. The comparison estimates express the corresponding proportions and their differences. These results should be interpreted as period-specific clinician-use measures, not as counts of patients treated or as clinical outcomes.

The registry also names a secondary effectiveness outcome concerning the predicted marginal probability of statin use being concordant with estimated cardiovascular risk. Results for that secondary outcome are not reported in the registry record, so the primary reach findings do not answer that separate effectiveness question.

7. Results Posted in the Registry

• Active Implementation: 52.7% (87/165) versus 29.2% (40/137) on control; risk difference 23.5 percentage points (95% CI 12.8 to 34.3), risk ratio 1.81 (1.34–2.43); unadjusted two-proportion z-test p = <0.001.
• Maintenance: 41.9% (54/129) versus 29.2% (40/137) on control; risk difference 12.7 percentage points (95% CI 1.2 to 24.1), risk ratio 1.43 (1.03–2.00); unadjusted two-proportion z-test p = 0.031.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary at the clinician level: a clinician either was or was not recorded as ever using CV Prevention Choice during the assessed period. The posted arm values are counts of clinicians with use, while the accompanying group sizes define the denominators. The registry describes the endpoint as a percentage, but the results also supply the counts and the unadjusted recalculations report proportions. This distinction matters: a count describes how many clinicians met the endpoint, whereas a proportion allows comparison between groups with different denominators.

What does the risk difference express?

A risk difference subtracts one group’s event proportion from another group’s event proportion. For active implementation versus usual care, the recalculated risk difference is 0.235. For maintenance versus usual care, it is 0.127. A positive estimate means that the observed proportion was higher in the implementation-period group than in the usual-care group. The estimate is an absolute contrast on the proportion scale; it is not a relative increase and does not by itself establish why the groups differed.

What does the confidence interval tell the reader?

A confidence interval describes the uncertainty around an estimated contrast under the assumptions of the statistical method. A narrower interval indicates greater precision; a wider one indicates less precision. The interval does not give a range that is guaranteed to contain the true effect, and it does not address sources of bias that the analysis did not account for. Here, the active-implementation interval runs from 0.128 to 0.343, while the maintenance interval runs from 0.012 to 0.241. Both intervals are above zero, but that fact does not eliminate uncertainty about the size of the differences or about their interpretation in this design.

How should the p-values be understood?

A p-value describes how compatible the observed data are with a specified null hypothesis under the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or practical importance of a difference. The pairwise p-values, <0.001 and 0.031, belong to unadjusted recalculations. The sponsor’s chi-squared p-value of < 0.001 applies to an overall comparison among the three groups. These tests address related but different questions, so their values should not be treated as interchangeable.

The recalculated risk differences are simple, unadjusted comparisons based on posted summary statistics. Such calculations do not automatically account for the randomized sequence structure, calendar time, clustering, repeated observations, or other possible covariates. General statistical principle: an adjusted model can be important when the design or data structure creates dependencies or imbalances, but the model and its assumptions need to be reported to evaluate that analysis. The specific adjustment strategy is not reported in the registry record.

Why can over-dispersion matter?

General statistical explanation: for binary outcomes, a basic model may assume that observations are independent and that the variability follows the model’s specified distribution. If clinicians’ outcomes are more alike within clinics or other groups than the model assumes, the observed variability can exceed the model’s expectation. This is called over-dispersion. Ignoring it can make standard errors too small and confidence intervals too narrow. The registry entries presented do not establish whether over-dispersion was assessed or whether clustering was incorporated into the sponsor’s analysis.

The registry reports a chi-squared method for the overall comparison, but does not specify further details such as whether any continuity correction, cluster adjustment, or covariate adjustment was used. The primary-analysis population is described by eligibility for a clinical encounter in each step, which means that inclusion depended on having such an encounter during that period. The record does not describe missing-data handling beyond the stated exclusion of clinicians without an eligible encounter.

In crossover and sequence-based studies, time and treatment period can be important because observations may be related across periods and because practice can change over calendar time. General statistical principle: an analysis should reflect the randomization unit and account for relevant dependencies in the data. The registry record does not provide enough information to assess these features in the reported sponsor analysis. The simple pairwise results therefore serve as unadjusted summaries, not replacements for a fully described design-based analysis.

10. Confidence Intervals and Precision

The confidence intervals express the precision of the unadjusted risk-difference estimates. For active implementation versus usual care, the estimate is 0.235, and its interval extends from 0.128 to 0.343. For maintenance versus usual care, the estimate is 0.127, and its interval extends from 0.012 to 0.241. Both intervals include a range of possible differences, rather than a single exact value.

The maintenance interval is closer to zero at its lower limit than the active-implementation interval. This indicates that the maintenance comparison is compatible with a smaller difference, as well as with larger differences within the interval. The active-implementation estimate is also uncertain: its interval does not specify one exact magnitude, and the upper and lower bounds should be read together with the point estimate.

Confidence intervals reflect sampling uncertainty under the calculation’s assumptions. They do not account for every potential source of uncertainty, including any unmeasured differences across periods, selection related to having an eligible encounter, or design features not represented in the simple recalculation. The registry record does not report an adjusted confidence interval for these comparisons. As a result, the intervals should not be read as resolving possible confounding, clustering, or time-related effects.

The p-values provide a related but different summary. A small p-value does not make an estimate more precise, and it does not mean that the observed effect is large or important. For interpretation, the estimated differences and their confidence intervals are more informative about magnitude and uncertainty than a threshold-based reading of statistical significance alone. The sponsor’s overall chi-squared test addresses a separate three-group question and does not provide a confidence interval for either pairwise contrast.

11. 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 effects, not the study’s original design calculations. The registry record does not report the trial’s original sample-size assumptions or justification. The illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They show planning for 100%, 75%, and 50% of the observed effect. The figures are participants per arm for 80% power and participants per arm for 90% power; they are not total events.

For the active-implementation comparison, the planning row for 100% of the observed effect gives 68 participants per arm for 80% power and 90 participants per arm for 90% power. Planning for 75% of the observed effect gives 118 participants per arm for 80% power and 157 participants per arm for 90% power. Planning for 50% of the observed effect gives 258 participants per arm for 80% power and 344 participants per arm for 90% power.

For the maintenance comparison, planning for 100% of the observed effect gives 224 participants per arm for 80% power and 299 participants per arm for 90% power. Planning for 75% of the observed effect gives 390 participants per arm for 80% power and 521 participants per arm for 90% power. Planning for 50% of the observed effect gives 856 participants per arm for 80% power and 1,146 participants per arm for 90% power.

In plain terms, the 80% column describes a planning target under which the assumed study would have an 80% chance of detecting the specified effect using the stated test assumptions; the 90% column uses a higher target probability. Smaller effects need more participants to detect under otherwise identical assumptions. These figures are planning illustrations, not observed power, and they should not be mistaken for the trial’s actual design plan.

12. 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 = 0.292; treatment proportion p₁ = 0.527; average p̄ = 0.410.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6955 = 1.3631.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6753 = 0.5683.
4. n = (1.3631 + 0.5683)² / (0.2353)² = 67.4, rounded up to 68 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 <- 0.291970802919708                          # control proportion
p1 <- 0.527272727272727                          # 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(4450914)
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 = 68 (80% power), 90 (90% power)
 75% of observed effect: n per arm = 118 (80% power), 157 (90% power)
 50% of observed effect: n per arm = 258 (80% power), 344 (90% power)
power.prop.test: 67.4 
Simulated power at n = 68 per arm: 0.799 (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.

13. Analyses Reported by the Sponsor

The registry reports a sponsor analysis using a chi-squared test across usual care, active implementation, and maintenance, with p< 0.001. This is an overall test of differences among the three groups. It does not, by itself, state the size of a particular pairwise contrast or identify which groups differ.

The pairwise risk differences and their confidence intervals are recalculated, unadjusted comparisons from the posted group counts. They answer narrower questions: active implementation versus usual care, and maintenance versus usual care. Their p-values are also unadjusted. Because the sponsor’s overall test and the pairwise recalculations do not test precisely the same contrast, their p-values should not be compared as if they were competing versions of the same analysis.

The registry record flags a discrepancy. Where there is a discrepancy, the sponsor’s own analysis takes precedence. The recalculations are useful as transparent summaries of the posted counts, but they do not replace the sponsor’s reported analysis or any analysis that accounts for the study’s sequence and period structure. The record does not describe enough of the sponsor’s model or assumptions to reproduce that analysis in full.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 16 outcome measures and 11 analyses. It identifies one secondary outcome: the predicted marginal probability of statin use being concordant with estimated cardiovascular risk. The primary outcome is clinician reach. Results for the named secondary outcome are not reported in the registry record.

Several comparisons are relevant to the primary outcome: the three groups can be compared overall, and implementation and maintenance can each be compared with usual care. The sponsor reports an overall chi-squared analysis, while the recalculated pairwise contrasts are unadjusted. The registry does not report whether a multiplicity adjustment was planned or used for multiple outcomes, comparisons, or analyses. Without that information, the pairwise p-values should be read as unadjusted results rather than as values adjusted to control the chance of false-positive findings across a family of tests.

The registry defines the primary analysis population by clinical encounters: clinicians without an eligible encounter during a step were excluded from that step. It does not report how many clinicians were excluded for this reason, how missing electronic-record use data were handled, or whether any imputation or sensitivity analysis was conducted. It also does not describe a broader intention-to-treat population for the primary outcome.

The record does not explain whether the same clinician could contribute to more than one period-specific group, or how any such repeated observations were handled. It also does not report whether the sponsor’s analysis adjusted for sequence, time period, or clinic-level clustering. These details are important for interpreting uncertainty and the relationship between comparisons, but they are not reported in the registry record. The posted estimates therefore support a limited reading of the defined clinician groups rather than a complete assessment of all analysis-population and missing-data decisions.

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

The primary results describe recorded use of CV Prevention Choice among clinicians who were eligible for assessment in each period. The counts were 40 of 137 in usual care, 87 of 165 during active implementation, and 54 of 129 during maintenance. The unadjusted recalculations show higher proportions in the two implementation periods than in usual care, with risk differences of 0.235 for active implementation and 0.127 for maintenance.

These findings concern reach, not clinical effectiveness. They do not establish that the tool changed patient treatment, improved risk communication, or altered cardiovascular outcomes. The secondary outcome concerning concordance between statin use and estimated risk is named in the registry, but its results are not reported in the registry record. The reach endpoint also does not reveal whether use occurred once or repeatedly, or whether the tool was used appropriately during a clinical conversation.

The period comparisons should be interpreted with the study’s sequence structure in mind. The registry lists different dates for the start of usual care and active implementation across the three sequences, and a shared date for entry into maintenance. The unadjusted comparisons do not show whether time trends, sequence, or other factors were taken into account. The sponsor’s reported overall chi-squared analysis should be distinguished from the pairwise recalculations.

The findings therefore support a descriptive conclusion about recorded clinician use across the listed periods, with uncertainty represented by the recalculated confidence intervals. They do not establish that implementation caused the differences, nor do they demonstrate a patient-level benefit. Claims beyond clinician reach require additional reported analyses and outcomes.

16. Why This Trial Matters Statistically

This study illustrates why implementation outcomes and clinical outcomes need to be distinguished. A behavioral tool may be designed to support shared decision making, but a reach measure asks whether eligible clinicians used it, not whether the conversations changed decisions or health. Measuring uptake can identify an important step in the pathway from implementation to patient outcomes, while also making clear what the measure cannot establish.

The sequence and period structure also make analysis design consequential. The registry reports three sequences with staggered transitions into active implementation and a common maintenance start date. Simple comparisons of group proportions can be informative descriptions, but they do not automatically account for calendar time, repeated clinician observations, or clustering within settings. A clear account of the randomization unit, analysis model, and handling of dependence is important for judging the precision and causal interpretation of results.

The sponsor’s overall chi-squared result and the recalculated pairwise estimates highlight the value of distinguishing omnibus tests from specific contrasts. The overall test addresses whether the groups differ collectively; pairwise risk differences communicate the magnitude of particular comparisons. Both can contribute to interpretation, but they are not substitutes for one another, and multiplicity decisions matter when many outcomes and analyses are considered.

Finally, the planning illustrations show how required sample sizes depend on the effect targeted and the desired power, while remaining separate from the trial’s original design assumptions. Taken together, these statistical issues are central to understanding what the registry results say about clinician reach and what remains uncertain about implementation effects and patient-level consequences.

17. Limitations

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

The primary endpoint is a clinician-level measure of ever using the tool during a period. It does not describe frequency, timing, quality, or context of use. The registry record does not report whether use was verified beyond electronic health record recording or whether clinicians and patients actually completed a shared decision-making process.

Eligibility depended on having at least one eligible encounter in each assessed step. That definition is stated, but the record does not report the number excluded for lacking an eligible encounter or evaluate how this period-specific eligibility may affect comparisons. The relationship between the enrollment figure of 112127 and the clinician counts used for the primary endpoint is also not explained in the registry record.

The reported pairwise estimates are unadjusted recalculations. The record does not give enough detail to determine how the sponsor’s analysis handled sequence, calendar period, possible repeated clinician observations, or clustering across the three health systems. It also does not report the randomization procedure, the original sample-size justification, multiplicity procedures, or missing-data methods. These omissions limit assessment of the design and of the uncertainty around the comparisons.

The registry names a secondary outcome about statin use concordance with estimated cardiovascular risk, but results for that outcome are not reported in the registry record. The posted primary results therefore do not establish whether clinician reach was accompanied by changes in treatment patterns or patient outcomes. The registry lists zero values for adverse-event reporting fields across sequences, but the fields show zero at-risk counts; those entries do not support a conclusion about safety or about the absence of adverse events.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Implementing Shared Decision Making (SDM) For Individualized CV Prevention (SDM4IP) — NCT04450914.
• Registry record last updated 2026-07-29; status last verified 2026-07.
• Results first posted 2026-07-29.
• 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.

21. Record Summary

NCT04450914 is a completed randomized crossover study of shared decision-making implementation for cardiovascular prevention, sponsored by Mayo Clinic. The registry records enrollment as 112127 and lists three sequences moving through usual care, active implementation, and maintenance. The primary endpoint is clinician reach, defined as the percentage of eligible clinicians who ever used CV Prevention Choice during a period.

Recorded use was 40 of 137 clinicians in usual care, 87 of 165 in active implementation, and 54 of 129 in maintenance. Unadjusted recalculated risk differences versus usual care were 0.235 for active implementation and 0.127 for maintenance. The sponsor’s reported overall chi-squared analysis had p< 0.001; the recalculations are pairwise and unadjusted, and the sponsor’s analysis takes precedence where results differ.

The registry does not report the original sample-size assumptions, a detailed statistical plan, missing-data procedures, or results for the named secondary outcome. The primary findings describe clinician tool use and do not establish patient-level effectiveness.