Clinical Decision Support to Reduce Opioid Prescribing at Discharge for Inpatients Undergoing Surgery (LESS Study): An Interrupted Time Series Analysis

Abstract

Background:

Unnecessary opioid prescribing following surgery is wasteful and expands the reservoir for non-medical use, thereby contributing to preventable morbidity and mortality. We used an interrupted time series design to evaluate whether implementing a system-wide clinical decision support (CDS) intervention reduced opioid prescribing at discharge.

Methods:

We included adult surgical patients hospitalized for at least 24 hours who had not received any opioids in the 24 hours prior to discharge, as prescriptions in this cohort are more likely to represent unnecessary opioid prescribing. The pre- and post-intervention two-year periods were 2/13/21-2/12/23 and 2/13/23-2/12/25, respectively. Our primary outcome was discharge oxycodone in morphine milligram equivalents (MME). Secondary outcomes included whether any opioids were prescribed, and if so, how much. Segmented regression models adjusted for confounders were used to assess the immediate and trend-level effects of the intervention.

Results:

Analyzed data included 10,422 pre- and 11,795 post-intervention discharges. Total oxycodone prescribed per discharge was 27.4 MME pre-intervention and 16.5 MME post-intervention. Oxycodone MME prescribed at discharge was significantly lower post-intervention, with a ratio of geometric means of 0.83 (95% CI: 0.76, 0.90; 1-tailed superiority P <0.001) for the level change but no difference in slopes (P=0.919). For secondary outcomes, 21% of discharges were prescribed any oxycodone pre-intervention versus 18% post-intervention, with a relative risk of 0.87 (95% CI: 0.79, 0.96) assessing the level change. For the discharges with a prescription, median MME [Q1, Q3] was lower after intervention than before (75 [38, 112] vs 112 [75, 150]), with a ratio of geometric means of 0.70 (95% CI: 0.65, 0.75).

Conclusions:

An automated real-time clinical decision support tool resulted in clinically significant reductions in oxycodone prescribed at discharge. Incorporation of similarly simple decision support tools in electronic health record systems may significantly reduce unnecessary opioid prescriptions at scale and better align with guideline-concordant care.

Introduction:

Opioid-based therapy is a fundamental aspect of pain management before, during, and after surgery. However, opioid prescriptions at discharge often fail to align effectively with patient and procedure-specific needs.¹ Studies indicate that 42 to 71% of surgical patients have unused opioids after discharge.² Unused postoperative opioids represent waste and increase their availability for nonmedical use.^3,4 Opioid-related deaths continue to pose a major public health concern, with more than 80,000 opioid-related deaths reported in 2022.⁵ Although the majority of opioid-related fatalities can be linked to non-medical synthetic opioids, many patients who develop an opioid use disorder were first exposed to prescription opioids, either diverted for non-medical use or misused due to excessive prescribing.⁶

In recent years, evidence-based pain management guidelines have been associated with significant reductions in excess post-procedural prescribing.^7–9 However, guidelines tend to lag behind procedural advancements, such as the emergence of less invasive techniques and more sophisticated methods of regional analgesia. As guideline modification continues to gain traction, the goal is to test whether published recommendations can be applied broadly across health systems, while continuing to address the individual variability in patient-specific analgesic needs.¹⁰ The most consistently associated and readily available patient-related variable associated with post-discharge opioid consumption in surgical patients admitted to the hospital is opioid intake within 24 hours before discharge.^11–14 Yet, translating such insights into clinical care poses challenges. Clinical decision support tools within electronic health record systems provide a means to communicate just-in-time information, assisting prescribers in formulating informed analgesic plans at discharge that are tailored to the patient’s analgesic needs. While not every patient may benefit from having such information displayed to their clinician,¹⁵ patients without any opioid needs in the 24 hours before discharge represent an obvious group likely to benefit from scalable interventions to avoid or minimize the prescription of post-discharge opioids.¹⁶

This study assesses the impact of an electronic health record-embedded clinical decision support (CDS) tool activated for surgical inpatients with zero opioid intake in the 24 hours before discharge. The tool’s purpose was to reduce prescriptions by targeting the most commonly prescribed opioid formulation (oxycodone 5mg tablets) and using real-time opioid intake information to provide targeted non-opioid or reduced oxycodone prescription suggestions at discharge. Using an interrupted time series (ITS) study design, we tested the hypothesis that the embedded CDS tool would lead to a reduction in the total amount of opioids prescribed to procedural inpatients at discharge. As secondary outcomes, we evaluated the durability of any change in prescribing, the proportion of discharges prescribed any versus no oxycodone, and the average amount of oxycodone prescribed to patients who received a prescription.

Materials and Methods

The Institutional Review Board approved this observational cohort study and waived the requirement for informed consent (IRB# 499-23EP). The manuscript was written according to the Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) guidelines¹⁷ and template for intervention description and replication checklist (TIDieR).¹⁸ We established a study protocol a priori, which was registered before conducting the analysis. (https://doi.org/10.17605/OSF.IO/ATND8)

Study Design and Cohort

Our analytic sample comprised adult surgical and procedural inpatients with zero opioid intake in the 24 hours preceding discharge. Included patients were admitted at least overnight to one of two hospitals part of a healthcare system in the Midwest United States between February 13, 2021, and February 12, 2025. Exclusion criteria included patients who received liposomal bupivacaine in the 24 hours before discharge and those on opioids before admission for indications related to chronic pain, cancer pain, opioid use disorder, palliative, or comfort care purposes. Additionally, patients admitted for less than 24 hours were excluded (Figure 1).

Figure 1.

Study Flow Diagram.

Baseline demographic variables for the discharge patient cohort included age, gender, ethnicity, race, rural residence (Rural-Urban Commuting Area codes),¹⁹ and payor status (Medicaid versus other). Clinical covariates included the procedural specialty (based on procedure type), emergent case classification, length of hospital stay, and pain score at discharge. Prescribing clinician description (non-physician, attending physician, or trainee physician) was captured for discharges with a prescription. Since we targeted clinician prescribing behavior rather than patient-reported consumption, we retained all patient discharges that met the inclusion criteria in the dataset, irrespective of multiple dates.

Intervention

Alongside an institutional workgroup, we identified the misalignment in opioid discharge practices as a target for intervention. With the support and approval of many operational teams (Surgical Services Operations Committee, Pain Steering Committee, Pharmacy Safety Committee), a pop-up alert was built and integrated into the electronic health record at the discretion of the Decision Support Advisory Team, Physician Advisory Committee, and Clinical Informatics Group. The tool was designed with the best intentions of adhering to the five “rights” of clinical decision support: right information, to the right person, in the right format, through the right channel, at the right time.²⁰ The intervention was operationalized as the effective date on which the clinical decision support tool was introduced into the electronic health record, February 13, 2023. The CDS tool was activated when a clinician attempted to prescribe an electronic prescription of oxycodone 5mg tablets in a patient who had no opioid intake recorded in the last 24 hours, regardless of physical location within the hospital. The 24-hour look-back period was calculated based on the timestamp of the order for pharmacy discharge medication reconciliation placed by the provider. In the United States, hydrocodone and oxycodone are the predominant opioids prescribed upon discharge from surgical encounters, with oxycodone prescriptions increasingly becoming the default choice.^1,21,22 During the CDS design and beta testing phase, oxycodone 5mg tablet prescriptions comprised 79% of all opioid prescriptions written at discharge to eligible patients. Hence, this formulation was chosen as the target for the CDS.

Acceptance of the alternative within the CDS tool pre-populated the order tab with one of two suggested ordering routes: 1) non-opioid therapy, including acetaminophen 1000mg every six hours as needed or ibuprofen 800mg every 8 hours as needed, or 2) a reduced opioid prescription amount (five tablets of oxycodone 5mg) (Figure 2). Cancellation in the CDS tool removed the opioids from the discharge orders, and continuation without altering the order bypassed the CDS tool. Response to the CDS did not affect further modification of orders before discharge, which remained at the discretion of the ordering clinician.

Figure 2. Electronic health record-embedded clinical decision support tool.

The tool was securely activated within a patient chart for clinicians attempting to prescribe oxycodone to procedural patients with no opioid intake 24 hours before discharge.

Outcomes

The primary outcome was the amount of oxycodone prescribed per discharge, expressed in morphine milligram equivalents (MME). We chose opioid dose in MME as the primary outcome, rather than the number of prescriptions, because the quantity prescribed, standardized as MME, captures the potential changes in dosing and strength that might not be reflected in prescription counts alone. We determined the CDS intervention would be considered effective if we found noninferiority on both the step change (i.e., any immediate reduction in amount of oxycodone prescribed just after the start of intervention) and slope (i.e., the direction of change over time), and superiority on at least one. We anticipated a priori that the effect of the CDS tool on the amount of oxycodone prescribed at discharge would be through a decrease in intercept and not in slope.

Secondary outcomes included whether a patient was prescribed any (vs. none) oxycodone at discharge, and the total amount of oxycodone 5mg tablets expressed in MME for those discharged with a prescription. Further exploratory analyses included evaluating the outcomes based on the type of clinician prescribing (non-physician, attending physician, or trainee physician), and the response action by the prescriber if exposed to a discharge CDS. All outcomes were captured during both the pre- and post-intervention periods and categorized into months.

Statistical Analysis

An interrupted time series design was employed for the primary analysis, with groups defined by the CDS tool deployment date: February 13, 2021, to February 12, 2023 (24 pre-intervention months) and February 13, 2023, to February 12, 2025 (24 post-intervention months). All statistical analyses were conducted using the R programming language (v4.4.1; R Core Team 2024). We used the following R packages for our analysis: tidyverse, sandwich, lmtest and glmmTMB.

Primary Outcome

The effect of the CDS tool on our primary outcome, prescribed oxycodone amount, was evaluated by conducting a confounder-adjusted segmented regression analysis,^23,24 with patient discharges as the unit of analysis. We fit a segmented regression model in which the outcome was log(total oxycodone MME prescribed at discharge + 1), and the covariates included number of days since start of the trial, a binary variable for whether the CDS tool was active or not, number of days since the CDS tool was activated (set to zero in the inactive period), and potential confounders such as demographic factors, patient insurance type and surgery type (see Table 1 for full list of potential confounders). Patients with missing data for any of these covariates were excluded from the analysis.

Table 1.

Cohort characteristics of enrolled patient discharges stratified by intervention period.

Characteristic	Pre-intervention (n = 10,537)	Post-intervention (n = 12,024)	Absolute Standardized Difference	Missing, n (%)
Age, years, median [Q1, Q3]	65 [53, 75]	66 [53, 75]	0.021	0 (0%)
Sex, n (%)			0.002	0 (0%)
Female	4823 (46%)	5492 (46%)
Male	5714 (54%)	6532 (54%)
Race, n (%)			0.045	263 (1.17%)
Black	949 (9%)	1057 (9%)
White	8582 (82%)	9592 (81%)
Other	920 (9%)	1198 (10%)
Ethnicity, n (%)			0.045	221 (0.98%)
Hispanic or Latino	678 (6%)	907 (8%)
Not Hispanic or Latino	9780 (94%)	10975 (92%)
Postal code, n (%)			0.026	0 (0%)
Urban	8012 (76%)	9007 (75%)
Rural	2525 (24%)	3017 (25%)
Primary insurance, n (%)			0.033	0 (0%)
Medicaid	1186 (11%)	1231 (10%)
Other	9351 (89%)	10793 (90%)
Emergent case, n (%)			0.027	0 (0%)
Emergent	653 (6%)	826 (7%)
Other	9884 (94%)	11198 (93%)
Procedural specialty, n (%)			0.071	0 (0%)
Cardiology and Pulmonary	2648 (25%)	3024 (25%)
Gastrointestinal	2016 (19%)	2099 (17%)
General	1748 (17%)	2116 (18%)
Neurological	903 (9%)	990 (8%)
Cardiothoracic	775 (7%)	964 (8%)
Orthopedic	660 (6%)	867 (7%)
Otolaryngologic, Plastic Surgery and Urologic	597 (6%)	679 (6%)
Obstetric or Gynecologic	534 (5%)	554 (5%)
Vascular	396 (4%)	415 (3%)
Other	260 (2%)	316 (3%)
Hospital LOS, median [Q1, Q3]	5 [3, 10]	5 [3, 10]	0.011	0 (0%)
Last pain score, mean (SD)	0.89 (1.83)	0.92 (1.84)	0.019	0 (0%)

Abbreviations: CDS – clinical decision support; LOS – length of stay

The regression coefficient for days since start of trial (${\beta }_1)$ estimates the pre-intervention slope over time for the outcome. The regression coefficient for the binary variable indicating whether the CDS tool was active or not (${\beta }_2$) estimates the difference in mean log oxycodone MMEs prescribed (or the ratio of geometric means when exponentiated) just after activating our intervention. Finally, the regression coefficient for days since start of intervention (${\beta }_3$) estimates the difference in slopes between the pre-intervention and post-intervention periods. In other words, ${\beta }_2$ represents the immediate effect of the decision support tool on the amount of oxycodone prescribed (i.e., a step change in mean MME), whereas ${\beta }_3$ represents the change in temporal trends (slopes) after the intervention is activated compared to the pre-intervention period. These were our two primary parameters of interest.^{23, 24}

The effect of the CDS tool on these two parameters was evaluated through a joint hypothesis test.²⁵ The intervention was deemed effective if it was noninferior to the pre-intervention period for both the step change and the slope, and superior on at least one of the two. The noninferiority (NI) margin for the intercept was a relative increase of 16.5% (the NI margin was set a priori to half of the minimal clinically important difference of 33% reduction, which was also specified a priori)^13,14 in the amount of oxycodone prescribed (in MME), which corresponded to a 1.165 ratio of geometric means. Based on clinical consensus of the study’s steering committee, the NI margin for the slope was conservatively set a priori to an absolute increase of 10% (e.g., if the slope in the control group is a ratio of geometric means per month of 1.1, then the slope in the intervention period cannot exceed 1.2). The one-tailed noninferiority tests were conducted at an alpha level of 0.025 (overall and for each test), with no correction for multiple testing, since it is an intersection-union test (i.e., both outcomes must be significant to claim the intervention is effective).

To preserve the type I error of the joint hypothesis test, superiority tests were conducted only if noninferiority was found on both outcomes (i.e., favoring intervention). The 1-tailed superiority tests were conducted at an overall alpha of 0.025, and the P-values and CIs were adjusted for multiple testing using Holm-Bonferroni correction. Thus, the overall type-I error rate for this joint hypothesis testing procedure was maintained at 2.5%.

Furthermore, we conducted two sensitivity analyses. In the first, we accounted for potential seasonality by additionally adjusting for calendar month as a categorical variable in our original segmented regression analysis model. In the second, we accounted for potential autocorrelation by updating our original segmented regression analysis model to include a random effect for time. More specifically, we included a random intercept for days since intervention (as a categorical variable) and assumed that the intercepts were correlated across time with a first-order autoregressive (i.e., AR(1)) structure. This correlation structure assumes that observations closer in time are more strongly correlated, with the correlation decreasing exponentially with time.²⁶

Secondary Outcomes

The effect of the CDS tool on the relative risk of any oxycodone prescribed at discharge was evaluated in a similar fashion as for the primary outcome by conducting a segmented regression analysis using a Poisson model with a log-link and robust variance estimator. We had planned to use a log-binomial model, but it failed to converge. The Poisson regression model (with robust variance estimation) is a suitable alternative to the log-binomial model for estimating relative risk.²⁷ Poisson regression models are generally used for estimating relative rates for count data, but in the special case of binomial data, the estimated relative rates can be thought of as relative risks. Robust variance estimates were used to account for the tendency of Poisson regression models to overestimate the variance when applied to binomial data. The noninferiority margin for the intercept was a 23.3% relative increase (i.e., a relative risk of 1.233), and for the slope, an absolute increase of 15%. We also evaluated the effect of the CDS tool on the amount of oxycodone prescribed in those discharged with a prescription (i.e., excluding all those not prescribed oxycodone) using segmented regression with a linear regression model. The NI margin for the intercept was a relative increase of 23.3%, and for the slope was an absolute increase of 10%.

Exploratory Outcomes

Exploratory outcomes were evaluated using descriptive summary statistics. We summarized the median amount of oxycodone prescribed in those discharged with a prescription, grouped by type of prescribing clinician. Additionally, for the subgroup of discharges where prescribers were exposed to the CDS when initiating a prescription, we calculated the median amount of prescribed oxycodone grouped by the type of prescriber action taken in response to the alert.

Post-hoc Analysis

The impact of the intervention on alternative opioid formulation and post-discharge prescribing was explored via two post hoc exploratory analyses, using a manually extracted 5% random sample of the discharges. First, we compared the rates of alternative opioid agents or strengths prescribed at discharge between pre- and post-intervention groups. Second, we assessed the incidence of post-discharge additional opioid prescriptions, defined as receipt of at least one additional opioid prescription on post-discharge days 1 through 30.

Sample Size Justification

We estimated the statistical power based on the primary outcome of the amount of oxycodone prescribed at discharge for a patient. The power analysis was carried out after the study was completed, but before the statistical analysis, using prespecified effect sizes. Based on our work and that reported by others, we defined a 33% relative reduction from our pre-intervention control period in prescribed discharge oxycodone MMEs across eligible patients (those with zero MME consumed in the 24 hours pre-discharge) as the minimal clinically important population difference.^13,14

We calculated the empirical power for the study using a bootstrapping approach in which we repeatedly sampled primary outcome data with replacement from the existing pre-intervention data and created a post-intervention dataset for which we had imposed the hypothesized treatment effect on the pre-intervention data. The power was then computed under the joint hypothesis testing framework described above, i.e., we tested for noninferiority on both the slope and the intercept and then if noninferiority was found on both, we proceeded to test for superiority on either parameter. This empirical approach enabled the accurate estimation of power for outcomes with non-standard distributions and also facilitated the incorporation of our joint hypothesis testing framework, including “automatically” adjusting for the correlation between the outcome variables.^28,29

Assuming a sample size of 10,416 discharges per group (based on a study time period of 48 months and an average of 434 per month), and an alpha of 0.025, we estimated from the bootstrap resampling that the study had 99.9% power to detect a reduction of 33%, and over 90% power to detect a reduction of 17%, in the amount of oxycodone prescribed near the start of the intervention compared to just before it began. Both scenarios assumed the slope remained unchanged after the intervention. The observed final analysis sample size was 10,422 discharges in the pre-intervention period and 11,795 discharges in the post-intervention period.

Results

Between February 13, 2021, and February 12, 2025, we identified a total of 22,561 eligible discharges. After excluding discharges with missing data, 22,217 discharges were included in the primary and secondary analyses, of which 10,422 occurred in the pre-intervention period, and 11,795 in the post-intervention period (Figure 1). Characteristics of all enrolled patients stratified by intervention period (before and after deployment of the clinical decision support tool) are summarized in Table 1.

Descriptive statistics for all eligible discharges were computed by simply aggregating the appropriate quantities across the pre- and post-intervention periods, which was appropriate and sufficient, as we did not observe a temporal trend (slope). Total oxycodone prescribed per discharge before the intervention was 27.4 MME, and after the intervention was 16.5 MME. The median [10th percentile (P10), 90th percentile (P90)] amount of overall oxycodone prescribed was 0 [0, 75] MME after the intervention, compared to 0 [0, 112] MME before the intervention (we report 10^th and 90^th percentiles as the data were extremely skewed). Fewer discharges were prescribed oxycodone (2,218; 18%) after the intervention compared to before the intervention (2,176; 21%). In discharges with a prescription, the median [Q1, Q3] oxycodone dose prescribed at discharge was 75 [38, 112] MME after the intervention compared to 112 [75, 150] MME before the intervention (Figure 3).

Figure 3. Distribution of prescribed opioid amounts stratified by intervention periods.

A) Bar chart showing proportion of discharges being prescribed any oxycodone before (n = 2,176) and after (n = 2,218) the intervention. B) Overlapping density plots showing the distribution of opioid amounts in the subgroup of discharges with a prescription.

Primary and secondary analyses

For our primary outcome of oxycodone dose prescribed at discharge (total n = 22,217), the post-intervention period was found to be noninferior on both the immediate step change (P < 0.001) and the relative slope change (P < 0.001), compared to pre-intervention trends (Table 2, Figure 4). There was an immediate reduction in total prescribed MME post-intervention (ratio of geometric means 0.83, 95% CI: 0.76, 0.90; 1-tailed superiority P <0.001), but no relative change in slope (estimated relative change in slope 1.00, 95% CI: 1.00, 1.01; 1-tailed superiority P = 0.919).

Table 2.

Primary and secondary analysis results.

	Pre-intervention	Post-intervention	Step change, ${\beta }_2$		Baseline slope, ${\beta }_1$	Relative slope change, ${\beta }_3$
			Estimate (95% CI)	1-tailed superiority P-value	Ratio of geometric means for opioid prescriptions per month	Estimate (95% CI)	1-tailed superiority P-value
Primary Outcome a			Ratio of geometric means
Oxycodone prescribed at discharge for all patients, MME, median [P10, P90]	0 [0, 112]	0 [0, 75]	0.83 (0.76, 0.90)	< 0.001	1.00 (0.99, 1.00)	1.00 (1.00, 1.01)	0.919
Secondary Outcome 1 b			Relative risk
Any oxycodone 5mg discharge prescription received, n (%)	2,176 (21%)	2,218 (18%)	0.87 (0.79,0.96)	0.004	1.00 (0.99, 1.00)	1.00 (1.00, 1.01)	0.865
Secondary Outcome 2 a			Ratio of geometric means
Discharge oxycodone prescription (MME) for those prescribed, median [Q1, Q3]	112 [75, 150]	75 [38, 112]	0.70 (0.65,0.75)	<0.001	0.99 (0.99, 1.00)	1.01 (1.00, 1.01)	> 0.999

Abbreviations: CDS – Clinical decision support tool; CI – Confidence interval; MME – Morphine milligrams equivalent; P – Percentile; Q – Quartile.

The step change parameter, ${\beta }_2$, represents the immediate change in the outcome just after the start of the intervention. The baseline slope is the pre-CDS tool intervention slope (i.e., ratio of geometric mean for opioid prescriptions per month before the activation of CDS tool). The slope change parameter, ${\beta }_3,$ represents the relative change in slope from the pre-CDS period to the post-CDS period. The parameter values were obtained from separate segmented regression models, adjusted for potential confounders including demographic factors, procedure type, hospital length of stay and pain score (see Table 1 for full list).

The effect of the CDS tool on these two parameters was evaluated through a joint hypothesis test. The intervention was to be deemed effective if it is found to be noninferior to the pre-intervention period on both the parameters, and superior on at least one of the two. Noninferiority was achieved on both parameters for all three outcomes (all P < 0.001) and is not reported in table. The table only displays p-values from the 1-tailed superiority tests conducted at an alpha of 0.025. The superiority test p-values were adjusted for multiple testing using the Holm-Bonferroni correction.

^aSegmented regression analysis was conducted using a linear regression model on the log-transformed outcome (+1), adjusted for the potential confounders listed in Table 1.

^bSegmented regression analysis conducted using Poisson regression model with robust variance to estimate the relative risk, adjusted for potential confounders listed in Table 1.

Figure 4. Segmented regression analysis for the primary outcome of oxycodone prescribed at discharge.

The plot shows prescription data aggregated by month. The black points represent the raw data. The gray line is the smoothed pre-intervention trend obtained from the segmented regression model, the blue line is the post-intervention trend (i.e., the effect of activating the CDS tool) and the red line is the counterfactual post-intervention (i.e., the predicted post-intervention trend if the CDS tool had not been activated). Results show a significant reduction in the geometric mean of prescribed opioid MME post- versus pre-intervention.

The results of our first sensitivity analysis, in which we accounted for potential seasonality, were similar to the primary analysis (Supplementary Figure 1). The post-intervention period was noninferior on both the step change (P <0.001) and the slope (P <0.001). Further, the post-intervention period was superior on the step change with an estimated ratio of geometric means of 0.84 (95% CI: 0.76, 0.92; 1-tailed superiority P <0.001), but not the slope, with a relative change in slope of 1.00 (95% CI: 1.00, 1.01; 1-tailed superiority P = 0.916). The results of our second sensitivity analysis, which accounted for autocorrelation, were also similar to those from our main model. It was superior on the step change, with an estimated ratio of geometric means of 0.81 (95% CI: 0.73, 0.90; 1-tailed superiority P <0.001), but not the slope, with a relative change in slope of 1.00 (95% CI: 0.99, 1.01; 1-tailed superiority P = 0.479). Adjustment for procedural specialty was not possible in this model due to convergence failure; otherwise, its structure paralleled the primary analysis.

For our secondary outcome of any oxycodone prescribed at discharge (n = 22,217), the post-intervention period was superior on the step change with an estimated relative risk of 0.87 (95% CI: 0.79, 0.96; 1-tailed superiority P = 0.004), but not the slope, with a relative change in slope of 1.00 (95% CI: 1.00, 1.01; 1-tailed superiority P = 0.865). It was found to be noninferior on both the step change (P <0.001) and the slope (P <0.001).

For the subset of discharges with an oxycodone prescription (n = 4,320), the post-intervention period was superior on the step change with an estimated ratio of geometric means of 0.70 (95% CI: 0.65, 0.75; 1-tailed superiority P <0.001), but not the slope, with a relative change in slope of 1.01 (95% CI: 1.00, 1.01; 1-tailed superiority P = 1.000). It was found to be noninferior on both the step change (P <0.001) and the slope (P <0.001).

Exploratory analyses

Pre-intervention, the median [Q1, Q3] amount of oxycodone prescribed (in those with a prescription) by attending physicians (n = 357) was 112 [75, 225] MME, whereas post-intervention (n = 143) was 75 [38, 112] MME. Pre-intervention, the median amount of oxycodone prescribed by resident or fellow physicians (n = 942) was 112 [75, 188] MME, whereas post-intervention was (n = 1,042) was 75 [38, 150] MME. Pre-intervention, the median amount of oxycodone prescribed by non-physicians (n = 877) was 105 [75, 150] MME, whereas post-intervention (n = 1,033) was 75 [38, 90] MME.

In the subset of discharges where prescribers were exposed to the CDS, those who chose to accept the tool’s prompt (N = 1,161; 46.1%) prescribed a median [Q1, Q3] of 38 [38, 75] MME oxycodone at discharge, those who chose to cancel (N = 394; 15.6%) prescribed 0 [0, 0] MME, and those who decided to continue without alteration (N = 965; 38.2%) prescribed 75 [38, 150] MME. A summarization of the response to the tool stratified by clinician role is in Supplementary Table 1.

Post-hoc analyses

We manually reviewed a random 5% sample of the discharges during the pre- (N = 527) and post-intervention (N = 602) period. We found that an alternative opioid or alternative oxycodone strength was prescribed at discharge 12 (2%) times before the CDS implementation and 21 (4%) times after the CDS implementation, signifying minimal workaround behavior. In a further analysis of additional opioid prescriptions between days 1-30 after discharge, we found that 22 (4%) patients in the pre-intervention group and 25 (4%) patients in the post-intervention group received an additional opioid prescription.

Discussion:

In this interrupted time series analysis, we evaluated the impact of an innovative electronic health record-embedded clinical decision support tool activated when clinicians attempted to prescribe oxycodone on discharge for postsurgical patients who consumed no opioids in the 24 hours before discharge. The implementation of the clinical decision support tool was associated with an immediate and sustained reduction in the discharge prescription opioid amount, resulting in a decrease in both the overall quantity prescribed and the proportion of patients receiving any prescription, as well as the amount prescribed for those who did receive a prescription. Using detailed electronic health record data, we found that the median dose of prescribed oxycodone MME was reduced by almost 35% from 112 [75, 150] MME before the intervention to 75 [38, 112] MME after the intervention, among discharges with a prescription. Importantly, in the years since opioid stewardship has improved, we have exemplified how precise, context-aware CDS tools can still help avoid perioperative overprescribing.^10,11

These findings contrast with our prior work, in which a more generalized best practice alert for 21,689 surgical inpatient discharges did not significantly reduce opioid prescribing.¹⁵ This divergence underscores the importance of maintaining precision in the design and implementation of clinical decision support tools, specifically in presenting the right information to the right person, in the right format, through the right channel, at the right time.²⁰ By more narrowly targeting patients demonstrating minimal opioid needs in the 24 hours before discharge, we designed a strategy that is medically justified, reduces ambiguity for prescribers, and increases the likelihood of adherence. Alternative approaches for other populations warrant further exploration. The observed lack of change in the slope after the intervention confirms that this tool established a new, lower baseline for prescribing, which may complement broader policy efforts to prevent excess opioids from entering circulation.^30,31 The fact that clinicians either accepted an alternative (N = 1,161; 46.1%) or removed the opioid order (N = 394; 15.6%) for the majority of discharges post-intervention further underscores the utility of nudges in promoting more judicious prescribing.

On a broader scale, electronic health records and decision support functions have become ubiquitous. Not all decision alerts are beneficial, whether due to the healthcare context, perceived irrelevance, or desensitization. There are several recent examples of innovative and rigorous decision support systems that did not garner the expected response.^32–34 One randomized trial of decision support in adults having noncardiac surgery with volatile anesthesia found that alerts for hypotension, Bispectral Index (BIS) <45, and minimum alveolar fraction of anesthetic < 0.8 (triple-low alert) had a nominal impact on clinician behavior and did not reduce 90-day mortality.³³ Similarly, a recently implemented clinician-facing prescribing opioid tool failed to reduce self-reported opioid use in the 4 weeks after discharge.³² Assuming that all clinical decision support will be beneficial without adequate validation may hinder care. To be impactful and circumvent alert fatigue, decision support tools should be designed with workflow integration, user engagement, and contextual relevance in mind.

The implications of a decision support tool such as the one described for healthcare practice, economics, and the ongoing opioid crisis are significant. Our findings demonstrate an effective mechanism for operationalizing previously well-described evidence-based opioid prescribing guidelines after discharge.^35,36 According to the National Health Interview Study, one in nine Americans underwent a procedure in 2018, a ratio that increases to almost one in five for persons 65 years or older and those with Medicare.³⁷ About 10 million discharges after inpatient surgery occur annually in the United States.³⁸ Of these, 3.6 million patients may be assumed to have not taken any opioids in the 24 hours before discharge.³⁹ While speculative, a similar clinical decision support tool implemented on a national scale could possibly reduce post-procedural oxycodone prescriptions by millions of tablets per year in the United States alone. Although the development of CDS integration comes with costs, the economic savings from reduced medication costs alone, coupled with the avoided costs of managing opioid-related adverse events and hospital readmissions, could be considerable.⁴⁰

Limitations

There are limitations to this study. Interrupted time series designs are generally unaffected by typical confounding, but are more influenced by time-varying confounders.⁴¹ Although we evaluated for seasonality, it is plausible that other simultaneous initiatives, rapidly changing risk factors, or natural events affected the outcome. However, no overt, major co-initiatives or campaigns were identified, and the significant immediate step-change coinciding with CDS implementation strongly implicates the intervention itself as the cause for reduced opioid prescriptions. But the absence of a temporally matched control group that could have informed a difference-in-difference approach represents a limitation.

Additionally, both excessive and inadequate opioid prescribing can lead to unintended consequences. While we demonstrate an immediate and durable reduction in oxycodone prescribing at discharge following the implementation of a targeted CDS tool, we do not account for patient-reported outcomes after discharge, hospital readmission rates for pain-related concerns, or supplemental opioid prescriptions past 30 days. However, we found similar rates of additional opioids prescribed on days 1-30 post-discharge in the pre- and post-intervention periods. If prescribers noticed a recurring theme of patients requesting additional opioids, we would have expected to see a slope change in the two-year post-intervention period. Longer-term follow-up, including quantitative opioid amounts and qualitative measures of patient-centered pain interference and physical function might be beneficial for assessing whether the effect is meaningfully sustained.

Conclusion

In summary, our study provides evidence that precise, context-aware clinical decision support tools integrated into electronic health record systems are powerful instruments for promoting judicious opioid prescribing and supporting broader public health goals in managing unnecessary discharge opioid prescriptions.

Supplementary Material

Supplemental Digital Content File

Abbreviation Key

CDS

Clinical Decision Support

ITS

Interrupted Time Series

MME

Morphine Milligram Equivalents

STROBE

Strengthening the Reporting of Observational Studies in Epidemiology

Q

Quartile