Analyzing a Controlled Trial of Multicomponent Delirium Prevention in Older Medical Inpatients
Student Name
School of Nursing and Health Sciences, Capella University
NURS-FPX4025: Research and Evidence-Based Decision Making
Dr. Instructor Name
Month Day, Year
Analyzing a Controlled Trial of Multicomponent Delirium Prevention in Older Medical Inpatients
Delirium is the most common serious complication of hospitalization for older adults, and on this unit it is also the one least reliably seen. On the 30-bed general medical unit that prompted this analysis, patients aged 70 or older accounted for 486 of 1,118 admissions in the two quarters ending June 30, and 84 of those 486 patients (17.3%) had at least one positive Confusion Assessment Method screen documented during the stay. That figure is a floor rather than an incidence, because screening was documented on only 71% of eligible shifts. The practice question behind this analysis is whether a structured nonpharmacological prevention program is worth building here, and the article selected to test that question is the multicomponent delirium prevention trial reported by Inouye et al. (1999).
The study is a prospective controlled clinical trial with individual matching, and naming the design accurately matters more than any number inside it. Patients aged 70 or older admitted to the general medicine service were cared for on an intervention unit or a usual care unit, and each intervention patient was matched to a usual care patient on age and baseline risk stratum rather than randomized (Inouye et al., 1999). The intervention was a six-part protocol targeting cognitive impairment, sleep deprivation, immobility, visual impairment, hearing impairment, and dehydration, delivered by trained volunteers and an interdisciplinary team. Delirium was assessed daily by trained interviewers using the Confusion Assessment Method, an instrument validated against psychiatrist diagnosis (Inouye et al., 1990). Matching narrows confounding on the matched variables only; it cannot balance the unmeasured ones the way randomization does.
The analytic sample was 852 patients, 426 in each group, at a single academic medical center. Eligibility required age 70 or older, admission to the general medicine service, and intermediate or high risk for delirium at baseline. Patients already delirious on admission were excluded, which is appropriate for a prevention question and is also the reason the trial says nothing about treating delirium once it has started. Patients in intensive care and on surgical services were outside the sampling frame, as were those unable to take part in daily interviews. The sample is therefore an older, medically ill hospital population, communicative enough to be interviewed every day, and every claim made below is bounded by that description rather than by the size of the sample.
Findings, Denominators, and the Measurement Window
Delirium developed in 9.9% of the intervention group and 15.0% of the usual care group, an odds ratio of 0.60 with a 95% confidence interval of 0.39 to 0.92 (Inouye et al., 1999). Two translations keep that number honest. The absolute difference is 5.1 percentage points, which puts the number needed to treat at roughly 20 patients for one additional patient to avoid a first episode, and the width of the confidence interval means the true effect could plausibly be far smaller than the point estimate. The odds ratio also overstates the risk ratio when an outcome is this common: the risk ratio here is about 0.66, not 0.60, so a reader who reports that the program cut delirium by 40% has already misread the statistic.
The trial also reported total days with delirium, 105 versus 161, and total episodes, 62 versus 90, both favoring the intervention. What it did not report is any significant difference in the severity of delirium once an episode began, or in the rate of recurrence (Inouye et al., 1999). That pattern is the most useful thing in the paper for this unit, and it is the finding most often dropped when the study is summarized secondhand. The program appears to change whether a first episode happens; nothing in these data shows that it changes how severe an episode becomes or whether it returns. A prevention claim and a treatment claim are different claims, and only the first one is supported here.
Both the outcome and its window belong to the index hospitalization. Delirium was ascertained daily from admission to discharge, so the trial reports nothing about delirium in the weeks after discharge, nothing about readmission, and nothing about longer-term cognitive trajectory. The denominator for every rate above is the matched patient, not the patient day, which means the results describe how many people became delirious rather than how much delirium occurred per unit of exposure. Any comparison this unit later draws against these figures has to use the same denominator and the same daily ascertainment, or the comparison is decorative rather than informative.
Limitations and What One Study Licenses
Four limitations bound this study, and the design is the first of them. Because grouping was by unit and by matching rather than by randomization, unmeasured differences between the two groups cannot be excluded, and staff on the intervention unit knew what they were delivering, which can shift both the care given and the detection of the outcome. The setting is a single academic hospital, so nothing here establishes that the effect travels to community units with different staffing. The intervention depended on trained volunteers, a resource many units do not have, which makes fidelity rather than efficacy the likely failure point in replication. The trial is also old enough that its usual care is not this unit's usual care, and an absolute risk difference measured against comparison care from that era is not a forecast of what would happen here.
Later evidence helps with direction while leaving magnitude open. A meta-analysis of 14 studies of multicomponent nonpharmacological interventions found a pooled odds ratio of 0.47 with a 95% confidence interval of 0.38 to 0.58 for delirium incidence, along with a reduction in falls (Hshieh et al., 2015). That consistency across settings is reassuring, but most of the pooled studies share this trial's non-randomized design, so the synthesis inherits the same confounding rather than correcting it. Current clinical reviews continue to place multicomponent prevention ahead of any pharmacological option for this population (Oh et al., 2017). The honest reading is that the direction of the effect is well supported and the size of the effect on any particular unit is not knowable in advance.
On that basis the study licenses a bounded action: pilot the six-protocol bundle here with a defined fidelity measure, and treat the published effect size as a hypothesis rather than a target. It does not license a projected percentage reduction in the business case, does not extend to intensive care or postoperative patients, and does not support any claim about shortening or softening delirium that has already begun. The evaluation plan follows from the study's own measurement choices: first positive Confusion Assessment Method screen per 100 admissions of patients aged 70 or older, screening compliance reported beside it as a denominator quality check, and 12 months of baseline recorded before any comparison is drawn (Polit & Beck, 2021).
References
Hshieh, T. T., Yue, J., Oh, E., Puelle, M., Dowal, S., Travison, T., & Inouye, S. K. (2015). Effectiveness of multicomponent nonpharmacological delirium interventions: A meta-analysis. JAMA Internal Medicine, 175(4), 512-520.
Inouye, S. K., Bogardus, S. T., Charpentier, P. A., Leo-Summers, L., Acampora, D., Holford, T. R., & Cooney, L. M. (1999). A multicomponent intervention to prevent delirium in hospitalized older patients. The New England Journal of Medicine, 340(9), 669-676.
Inouye, S. K., van Dyck, C. H., Alessi, C. A., Balkin, S., Siegal, A. P., & Horwitz, R. I. (1990). Clarifying confusion: The Confusion Assessment Method. A new method for detection of delirium. Annals of Internal Medicine, 113(12), 941-948.
Oh, E. S., Fong, T. G., Hshieh, T. T., & Inouye, S. K. (2017). Delirium in older persons: Advances in diagnosis and treatment. JAMA, 318(12), 1161-1174.
Polit, D. F., & Beck, C. T. (2021). Nursing research: Generating and assessing evidence for nursing practice (11th ed.). Wolters Kluwer.
How this NURS FPX 4025 Assessment 1 example is structured
This NURS FPX 4025 Assessment 1 example follows the order the analysis itself has to follow. The opening page sets the practice question and the local numbers that made one study worth reading, then names the article and its design before any finding appears, because a finding you cannot place inside a design is not evidence yet. The second page reports results with their denominators and their measurement window, separates the outcome that reached significance from the outcomes that did not, and converts the odds ratio into plain risk language. The third page carries the limitations and the verdict: what a single non-randomized trial licenses on a medical unit, and what it does not. Students in the Capella University RN-to-BSN course Research and Evidence-Based Decision Making are graded on exactly that last distinction.
NURS-FPX4025 Assessment 1 questions, answered
Which article should I analyze for NURS FPX 4025 Assessment 1?
Pick a single primary research study, not a review or an editorial, that answers a question you actually meet in practice. It should be peer reviewed, report its own data, and have a design you can name and a sample you can describe. If you cannot state the design in one sentence after reading the methods, choose a different article.
Does the analysis have to be critical, or can I say the study was well done?
Analysis is not fault-finding. A strong paper can conclude that a study was well conducted and still name what its design cannot rule out. What loses credit is a paper with no limitations at all, or one that lists generic flaws such as small sample size without saying what that flaw does to the conclusion you are drawing from it.
How do I write about statistics without a statistics background?
Report what the study reported, then translate it. Give percentages with their denominators, state the confidence interval when one is published, and convert a ratio into an absolute difference so a reader can see the size of the effect. Say association when the design was observational. That care is what the course assesses, not advanced analysis.
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