Electronic prescribing and patient safety: a rigour-stratified systematic review of medication error, adverse drug events, workflow, and communication

Abstract

Background

Electronic prescribing is promoted to improve medication safety. Whether its benefit differs between process failure and patient harm is rarely asked.

Objective

To synthesise the evidence on electronic prescribing and medication error, adverse drug events, workflow and communication against the designs able to establish each.

Methods

We searched PubMed, Scopus, Web of Science, CINAHL, Embase and ProQuest (1994 to 2024, English), reporting to PRISMA 2020 and PRISMA-S. Risk of bias was assessed at domain level with design-matched tools. Non-poolable metrics precluded meta-analysis; findings were synthesised following SWiM.

Results

Forty studies were included, 31 quasi-experimental. None of the 31 was at low risk of bias; 27 moderate, four serious. Twenty-nine reported medication error, most a reduction of 20% to 98%. Four could be read against background change: the reduction held in three, and in one exceeded the crude difference, errors having risen beforehand. Three others had a concurrent comparison only. The remaining 22 measured no trend, so magnitude is uninterpretable. No design able to test an effect on harm showed one. Eight studies documented error classes introduced by the system, two quantifying them at 68% and 35% of residual errors. Workflow effort was redistributed rather than reduced, and communication disrupted short-term, nurses most affected.

Conclusions

Electronic prescribing reduces measured medication errors; the reduction holds in three of the four studies able to test it. An effect on patient harm has not been demonstrated. Certainty was very low for both quantitative outcomes, low for workflow, moderate for communication.

Highlights

• •Electronic prescribing reduces medication errors in 3 of 4 testable designs.
• •No design able to support a causal claim about harm has shown one.
• •Every error subtype fell except the type most associated with harm.
• •No quasi-experimental study was at low risk of bias; four were serious.
• •22 of 29 error studies measured no trend, so magnitude is uninterpretable.

1. Introduction

Medication-related harm is among the most common and most preventable threats to patient safety worldwide. The World Health Organization (WHO) estimates that half of all preventable harm in medical care is medication-related, a quarter of it severe or life-threatening, and that the global cost of medication errors approaches US$42 billion annually.¹ In response, the WHO launched its third Global Patient Safety Challenge, Medication Without Harm, in 2017, setting the goal of halving severe avoidable medication-related harm within five years.1, 2 Prescribing is the stage of the medication-use process at which many of these errors originate, and prescribing errors are consistently among the most frequent and most consequential error types.²

A medication error is a preventable event that may lead to inappropriate medication use or patient harm while the medication is under the control of a health professional, patient, or consumer.² An adverse drug event (ADE) is an injury resulting from a drug-related intervention.2, 3 The distinction is analytically important. A medication error is a process failure that may never reach the patient. An adverse drug event is an outcome: actual harm. The two are routinely conflated in the literature, but an intervention can reduce the former without altering the latter. The clinical value of any prescribing technology rests on its effect on harm, not on error counts.³

Throughout this review, electronic prescribing serves as the umbrella term for systems in which prescribers enter and transmit medication orders electronically. It covers computerised provider order entry (CPOE), where the prescriber enters orders directly within the hospital system, and e-prescribing systems that transmit prescriptions electronically to a dispensing pharmacy, in each case with or without integrated clinical decision support (CDSS). Findings specific to order entry without decision support, or to a decision-support component alone, say so. Standalone decision-support tools not integrated with prescribing fall outside the scope of this review.

These systems address the well-documented vulnerabilities of paper-based prescribing: illegibility, omission, transcription loss, and patient misidentification. The foundational evidence was encouraging. In a landmark before-after study at a US academic hospital, Bates and colleagues reported that CPOE with decision support reduced serious medication errors by more than half.⁴ An influential early synthesis by Kaushal, Shojania and Bates concluded that CPOE and CDSS could substantially reduce error rates.⁵ These results, reinforced by national policy initiatives, drove rapid and widespread adoption.

The picture that subsequently emerged was more complicated. Implementation repeatedly generated new, technology-specific failure modes. Koppel and colleagues documented that a widely used CPOE system facilitated 22 distinct types of medication error, arising from fragmented information display and interfaces misaligned with clinical work.⁶ Ash and colleagues described a broader class of unintended consequences of health information technology.⁷ Han and colleagues reported a significant increase in mortality among critically ill children after rapid CPOE implementation at a tertiary paediatric hospital.⁸ Electronic prescribing is not a self-evidently beneficial technology. Its effects are contingent on design, implementation, and setting.

A substantial body of primary studies has accumulated, and several systematic reviews have summarised it. The dominant conclusion has been favourable: electronic prescribing reduces medication errors.5, 9, 10 There are two features of this literature that remain inadequately addressed. First, the reported magnitude of benefit varies enormously, from marginal reductions to near-total error elimination. The span is so wide that any single summary estimate conceals more than it reveals. Reviews have generally treated this variation as clinical heterogeneity to be noted, not as a phenomenon to be explained. Second, the designs producing these estimates differ profoundly in their capacity to attribute change to the intervention rather than to secular trend, regression to the mean, co-intervention, or reporting artefact. The field is dominated by uncontrolled before-after studies. By construction, these cannot separate the intervention's effect from concurrent change. Yet their estimates are pooled or tallied alongside those of far more rigorous designs as though equivalent. The most methodologically careful recent syntheses have reached more guarded conclusions. A meta-analysis of electronic prescribing strategies found inconsistent effects on patient outcomes and rated the evidence as predominantly low or very low quality.⁹ An earlier rigorous review found benefit confined largely to preventable adverse drug events rather than actual harm.¹⁰

These two gaps are connected, and that connection was the subject of this review. If the apparent size of benefit depends on whether the study design can separate the intervention from background change, then the wide effect range is not unexplained heterogeneity. Much of it would be methodological in origin. The headline conclusion that electronic prescribing substantially improves medication safety would then rest disproportionately on the designs least able to support it. Two questions follow: (1) what do the designs capable of separating the two actually show, and (2) does the answer differ between process failure and patient harm? This review examined the evidence through a single analytic lens: whether a study can separate the intervention from change that would have occurred anyway. Four studies can do so, and these carry the primary analysis. The remaining studies fall into design-rigour tiers, which describe the evidence base rather than drive the inference. The synthesis covers four patient-safety domains: (1) medication error, (2) adverse drug events, (3) workflow, and (4) inter-professional communication. Risk of bias enters the synthesis as an analytic input rather than as a descriptive appendix. To our knowledge this is the first synthesis in this field to separate the evidence on process failure from the evidence on realised harm and to read each against the designs capable of establishing it.

2. Methods

2.1. Protocol and registration

The review was conducted and reported in accordance with PRISMA 2020,¹¹ with the search reported to PRISMA-S.¹² It was registered with PROSPERO on 7 October 2024 (CRD42024570480). The completed PRISMA 2020 checklist is provided as Supplementary note S6 and the PRISMA-S search-reporting checklist as Supplementary Table S5.

The conduct departed from the registered protocol in four respects. The timing of an amendment bears on how it should be read. For each, it is stated below whether the change was applied before or after data extraction and inspection of the outcome data.

First, the eligible publication window was extended from the registered “2000 to present” to 1994 to 2024. This was applied at the search stage. All six database searches were run between 20 and 30 September 2024 with an explicit 1994 to 2024 date filter, before screening and before any extraction. The filters as executed are reproduced in Supplement S1. The foundational electronic-prescribing safety literature dates to the mid-1990s. Excluding it would have biased the evidence base toward later and more mature systems.

Second, the registered protocol named “traditional methods” as the comparator in its objectives but “not applicable” under eligibility. This is a contradiction internal to the registration rather than a change of conduct. The operative comparator throughout was paper-based prescribing or a less integrated electronic system. Studies without a separate comparison group were retained only where they reported pre- and post-implementation outcomes.

Third, the registered random-effects meta-analysis was not performed. This decision was taken after data extraction. The reported effect metrics proved non-poolable across inconsistent denominators, error definitions and time windows. Pooling would have produced a precise summary estimate from clinically and methodologically incompatible data. A synthesis without meta-analysis was conducted instead. The registered subgroup and sensitivity analyses presupposed a pooled estimate and were correspondingly not run.

Fourth, the registered single appraisal tool (JBI) was replaced in reporting by a design-matched framework: ROBINS-I for non-randomised intervention designs, Newcastle-Ottawa for the one concurrent-comparison cohort study, MMAT for the mixed-methods studies and the cross-sectional process evaluations, and the JBI checklist for qualitative studies. Design-matched appraisal was in fact carried out during the review. The change was to which appraisal was reported as primary, and it was settled after extraction. No single instrument validly appraises the range of designs that met inclusion. A fit-for-purpose instrument per design seems the more defensible choice.

The third and fourth amendments were therefore made after the outcome data had been inspected. This is stated plainly here. Post hoc changes of this kind carry a risk of analytic flexibility, and the synthesis might reasonably be weighed accordingly.

2.2. Eligibility criteria

Eligibility was framed using PICO. Population: physicians, nurses, pharmacists, and patients in healthcare settings. Intervention: e-prescribing systems, CPOE, integrated CDSS within e-prescribing, and direct electronic transmission; standalone CDSS, non-prescribing EHR components, and manual prescribing were excluded. Comparator: paper-based prescribing or a less-integrated electronic system. Outcomes: medication error, adverse drug events, workflow and care coordination, and inter-professional communication. Setting: hospitals (inpatient/outpatient), nursing homes, and day-care centres; primary and community centres excluded. Designs: controlled trials, cohort, case-control, cross-sectional, quasi-experimental, qualitative, and mixed-methods; case reports/series, editorials, conference abstracts, and reviews excluded. Language/dates: English, 1994–2024.

2.3. Information sources and search

A three-step strategy was used: an initial limited search of PubMed and CINAHL identified candidate terms; the full strategy then combined population, intervention, and outcome concept blocks (using MeSH, Emtree, and CINAHL subject headings alongside title/abstract/keyword terms) across PubMed, CINAHL, Embase, ProQuest, Web of Science, and Scopus. Searches were run between 20 and 30 September 2024 (last search 30 September 2024), limited to English-language records published 1994–2024. The searches returned 1565 records in PubMed, 1534 in Embase, 1053 in Web of Science, 843 in Scopus, 625 in ProQuest, and 247 in CINAHL (5867 in total). The full line-by-line strategy for each database is provided in Supplement S1.

2.4. Study selection

Records were exported from all six databases, de-duplicated, and screened in Rayyan. Titles and abstracts were screened against the eligibility criteria. Records passing this stage were advanced to a second, full-text screening stage within the same tool, so that decisions at both stages are held in a single screening record. Screening was performed independently by two reviewers (RJ, SP), with a third reviewer arbitrating disagreements that could not be resolved by discussion, as registered. Counts at each stage in Fig. 1 are taken from the screening record.

Fig. 1.

PRISMA 2020 flow diagram of study identification, screening, and inclusion.

2.5. Data extraction

Data were extracted into a piloted standardised form capturing identifiers, country, design, setting and population, intervention and comparator, outcome domain, effect metric, and direction of effect. Extraction was carried out by one reviewer (RJ) and verified for accuracy and completeness against the source reports by a second (SP), with disagreements resolved by discussion and a third reviewer consulted where consensus could not be reached, as registered. No automation tools were used at this stage.

The extracted fields for every study are reported in Supplementary Table S7.

2.6. Risk-of-bias assessment and design-rigour tiers

Risk of bias was assessed with the instrument matched to each design rather than with a single tool: ROBINS-I¹³ for the 31 non-randomised intervention studies (uncontrolled before-after, controlled before-after, interrupted time-series, stepped-wedge and segmented time-series); the Newcastle-Ottawa Scale¹⁴ for the one concurrent-comparison cohort study; MMAT¹⁵ for the three mixed-methods studies and the two cross-sectional process evaluations; and the JBI checklist¹⁶ for the three qualitative studies. Each ROBINS-I domain was judged separately. The overall judgement for each study is its least favourable domain judgement, as the instrument specifies. Domain-level judgements for every study are reported in Supplementary Table S3.

Separately from appraisal, each quantitative study was assigned to a design-rigour tier. Tiers were assigned on the study design alone, and specifically on whether the design can separate change following implementation from change that would have occurred anyway:

Tier 1: designs that model change across multiple time points rather than a single before-and-after contrast, namely interrupted time-series, stepped-wedge and segmented time-series. Two of the three studies in this tier estimate the pre-implementation trend. The third is a four-period series with a single pre-implementation measurement and cannot; §3.4.1 identifies it and states what its structure does and does not establish.

Tier 2: designs with a concurrent comparison group followed through both study periods, with baseline equivalence demonstrated between groups.

Tier 3: uncontrolled before-after designs, with neither a concurrent control nor trend modelling. Studies with a concurrent comparison that did not demonstrate baseline equivalence, or in which allocation was by unit or by prescriber rather than by patient, were also assigned to Tier 3, and their comparison data are reported alongside the intervention estimate. Three studies fall into this category. Westbrook 2012¹⁷ ran three concurrent control wards of differing specialty, without randomisation or matching, and at its second hospital no control ward was available for the two intervention wards there. Huertas 2006¹⁸ allocated by prescriber, so prescriber effects are confounded with the intervention. Urtasun 2022¹⁹ compared a children's hospital against a general hospital of different case mix. Only King 2003²⁰ met the Tier 2 criterion, having shown the intervention and control wards indistinguishable before implementation (ratio 0.93, 95% CI 0.76 to 1.13).

Cross-sectional, mixed-methods and qualitative studies are process evaluations. They are not assigned a tier and are synthesised separately for the workflow and communication domains.

Tier and risk of bias are distinct and are reported separately throughout. A design capable of adjustment might still be executed in a way that admits substantial bias. A carefully conducted uncontrolled before-after study remains unable to perform that adjustment at all. Neither measure is derived from the other, and both are shown for every study in Table 1. A moderate ROBINS-I rating does not make an uncontrolled before-after estimate suitable for causal inference. The limitation is a property of the design and not of how well the study was conducted. Study design classification and risk-of-bias assessment were performed independently by two reviewers, with disagreements resolved by discussion and arbitration by a third. Where reclassification arose during revision from re-examination of the full texts, the assessment was made by one reviewer and confirmed by a second. Four studies were reclassified on this basis: Wimmer 2023,²¹ Westbrook 2012,¹⁷ Urtasun 2022¹⁹ and Huertas 2006.¹⁸

Table 1.

Characteristics, risk of bias and direction of effect for the 40 included studies.

#	Ref	Study	Country	Design	Tier	RoB tool	RoB judgement	Outcome domain(s)	Direction of effect and basis
1	28	AlAzmi 2019	Saudi Arabia	Uncontrolled before-after (historical control)	3	ROBINS-I	Serious	ME (drug-related problems)	Reduction, crude (44.8% to 35.8%); drug-choice problems rose
2	21	Wimmer 2023	Germany	Uncontrolled before-after	3	ROBINS-I	Moderate	ADE (primary); potential ME	ADE null; potential ME reduced (1.69 to 0.71 per patient)
3	25	Potts 2004	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	ME; potential ADE	ME reduction, crude (95.9%); potential ADE reduction 41%
4	26	Satir 2023	Switzerland	Uncontrolled before-after	3	ROBINS-I	Serious	ME (prescribing)	Reduction, crude (78.4 to 25.1 per 100); dosing errors unchanged
5	19	Urtasun 2022	Argentina	Controlled before-after (concurrent control hospital; baseline equivalence not demonstrated)	3	ROBINS-I	Moderate	ME (prescribing)	Reduction, crude (29.1 to 19.9 per 100)
6	40	Sin 2021	Hong Kong	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (prescribing)	Reduction, crude (6.7% to 3.9%)
7	41	Kenawy 2019	Egypt	Uncontrolled before-after	3	ROBINS-I	Moderate	ME; workflow	ME reduction, crude, modest (28.3% to 26.3% per medicine); omission and indication errors rose
8	34	Al-Sarawi 2019	Australia	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (prescribing)	Reduction, crude (67.7 to 2.8 per 100); duplications rose
9	36	Mills 2017	UK	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (discharge)	Reduction, crude (99.4% to 23.3% of patients; 84% to 23% excluding omitted allergy information, which the system made mandatory)
10	42	Hitti 2017	Lebanon	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (discharge)	Reduction, adjusted for covariates but not for secular trend (OR 0.40, 95% CI 0.35 to 0.47; crude 67.7% to 45.5%); incorrect strength rose
11	43	Yugandhar 2017	India	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (discharge)	Reduction, crude (36% to 11% of prescriptions)
12	29	Kazemi 2011	Iran	Uncontrolled before-after, 3 periods	3	ROBINS-I	Serious	ME (prescription and transcription)	No reduction from order entry alone; reduction only after CDSS added
13	44	Hodgkinson 2017	Australia	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (prescribing and dispensing)	Reduction, crude (95% to 13.6% of patients)
14	45	Cordero 2004	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (dosing)	Reduction, crude (13% to 0); dosing was the only class measured
15	54	McMullen 2015	USA	Mixed-methods	P	MMAT	High quality	Workflow; communication	Pharmacy workflow improved; prescriber contact reduced
16	33	Ayatollahi 2015	Iran	Mixed-methods	P	MMAT	Low quality	Workflow; communication	Mixed; nurses more positive than physicians
17	46	Hou 2013	Taiwan	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (dosing)	Reduction, crude, with dosing decision support (2.25% to 0.91%)
18	31	Hoonakker 2013	USA	Cross-sectional, 3 rounds	P	MMAT	High quality	Communication	Short-term decline then recovery; nurses rate quality lower than prescribers at every round, including baseline
19	27	Jozefczyk 2013	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (opportunity for error)	Reduction, crude (8.5% to 0.5% of error opportunities)
20	55	Chapman 2012	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	Workflow	Partial: verification faster, total task time unchanged
21	47	Abbass 2011	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (administration process)	Reduction, crude (117 to 18 errors)
22	30	van Doormaal 2009	Netherlands	Interrupted time-series	1	ROBINS-I	Serious	ME; preventable ADE	ME reduction, adjusted (40.3-point immediate reduction; crude 55% to 17%); preventable ADE null after adjustment
23	48	Jani 2008	UK	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (completeness, legibility)	Reduction, crude (77.4% to 4.8%); dominated by missing information
24	39	Donyai 2008	UK	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (prescribing)	Reduction, crude (3.8% to 2.0%)
25	56	Beuscart-Zéphir 2005	France	Qualitative	P	JBI	High quality	Communication	Negative: reduced doctor-nurse collaboration
26	52	Upperman 2005	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	ADE (all and harmful)	All ADE null (p = 0.3); harmful ADE borderline reduction (p = 0.05)
27	20	King 2003	Canada	Retrospective controlled cohort (concurrent comparison wards)	2	NOS	Adequate (7 stars)	ME; ADE; potential ADE	ME reduced 40% vs control; ADE null; potential ADE fell more on controls
28	58	Mohsin-Shaikh 2023	UK	Qualitative	P	JBI	High quality	Communication	Negative: reduced pharmacist ward presence and direct interaction
29	38	Franklin 2019	UK	Stepped-wedge	1	ROBINS-I	Moderate	ME (prescribing)	Crude 7.8% to 6.0%; null after adjustment for clustering
30	59	Pontefract 2018 (qual)	UK	Qualitative	P	JBI	High quality	Communication; workflow	Mixed: pharmacist communication load rose; record access improved
31	51	Pontefract 2018 (quasi)	UK	Uncontrolled before-after, 3 sites	3	ROBINS-I	Moderate	ME (high-risk)	Reduction, crude, at 2 of 3 sites; no change at the third
32	53	Holdsworth 2007	USA	Uncontrolled before-after	3	ROBINS-I	Moderate	Preventable ADE; potential ADE	Reduction, crude (RR 0.56 and 0.37); preventable ADE is realised harm, against a historical comparator
33	17	Westbrook 2012	Australia	Controlled before-after (3 concurrent control wards at 1 of 2 hospitals; baseline equivalence not demonstrated)	3	ROBINS-I	Moderate	ME (prescribing)	Reduction, crude (total errors down 66.1%, 57.5% and 60.5% across 3 wards); driven by procedural errors, clinical errors unchanged
34	32	Hanauer 2013	USA	Cross-sectional time-and-motion	P	MMAT	Low quality	Workflow	Positive: less task fragmentation; direct care time unchanged
35	49	Armada 2014	Spain	Uncontrolled before-after, 3 phases	3	ROBINS-I	Moderate	ME; workflow	ME reduction, crude (44.8% to 0.8%); 74% reported higher workload
36	18	Huertas 2006	Spain	Concurrent non-randomised comparison, allocation by prescriber	3	ROBINS-I	Moderate	ME (chemotherapy)	Reduction, crude (100% to 13% of prescriptions); allocation by prescriber
37	50	Voeffray 2006	Switzerland	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (chemotherapy)	Reduction, crude (15% to 5%)
38	37	Bates 1999	USA	Segmented time-series, 4 periods (single pre-implementation measurement)	1	ROBINS-I	Moderate	ME; non-intercepted serious ME; ADE	ME reduction, 81% across four periods (p < 0.0001); total ADE null (p = 0.09); missed doses rose
39	35	Hernandez 2015	France	Uncontrolled before-after	3	ROBINS-I	Moderate	ME (prescribing)	Reduction, crude (30.1% to 2.4%)
40	57	Pirnejad 2008	Netherlands	Mixed-methods	P	MMAT	High quality	Communication; legibility	Legibility improved; nurse-physician synchronisation disrupted

2.7. Synthesis

The primary studies reported effects in heterogeneous and non-convertible metrics. A pooled estimate would have been neither valid nor interpretable, and meta-analysis was not undertaken. Findings were synthesised following the SWiM reporting guideline.²² The standardised metric was the direction of effect, coded against rules specified in advance of coding:

Large benefit: a relative reduction of 50% or more on the study's primary error or event metric.

Modest benefit: a statistically supported reduction of less than 50%.

Mixed: a reduction on some error classes accompanied by a significant increase on others, or benefit at some study sites and not others.

Null: no statistically supported difference on the primary metric after the study's own adjustment.

Conditional: benefit present only under a specified condition, such as the addition of decision support.

Adverse: a statistically supported increase in errors or events.

Statistical significance was required for any code other than null. Absolute change, clinical relevance and direction across multiple error types were not used to assign the primary code. These are reported alongside each study in the counter-findings column of Supplementary Table S7, so that a reader can weigh them independently of the code.

Where a study reported an analysis adjusted for the underlying trend or against a concurrent comparison group, the adjusted estimate was coded. Otherwise the crude before-after difference was coded. The basis of the code is stated for every study in Supplementary Tables S2 and S7. Only designs with a concurrent control or a modelled trend can produce an adjusted estimate, so the basis of the code is not independent of the design. Adjustment removes the underlying trend, which may run in either direction, so an adjusted estimate is not necessarily smaller than a crude one; this is examined in §3.4.2. Process and harm outcomes were synthesised separately, and each was read against the designs capable of establishing it. The cross-tabulation of direction against design-rigour tier is presented as a description of the evidence base rather than as the basis of the inference.

Certainty of evidence was rated by outcome using GRADE²³ and, for the qualitative communication finding, GRADE-CERQual.²⁴ Ratings and the reasoning for each are given in Supplementary Table S4.

3. Results

3.1. Study selection

The database search yielded 5867 records. After removal of 2460 duplicates, 3407 records were screened by title and abstract and 3277 were excluded. Of the 130 reports advanced to full-text screening, 11 were not retrieved or not assessed, leaving 119 assessed for eligibility. Seventy-one were excluded at full text and 48 met the eligibility criteria. A further eight reports were set aside after eligibility assessment, leaving 40 studies included (Fig. 1).

Reasons for exclusion at full text were recorded in the screening tool for 41 of the 71 excluded reports: ineligible outcome (n = 34), ineligible study design (n = 31), background article (n = 3), ineligible population (n = 3), ineligible study duration (n = 1) and ineligible drug (n = 1); some reports were excluded for more than one reason. There is no record of a reason for the remaining 30 reports. Of the eight reports set aside after eligibility assessment, six were set aside at the data-extraction stage: Cheng 2003, Colpaert 2006, Devine 2010, Fayaz-Bakhsh 2014, Gandhi 2005 and Nanji 2014. The other two were excluded during revision on re-examination of their full texts: Tran 2019, in which both study periods prescribed electronically, so that the study does not compare electronic with non-electronic prescribing, and Almohammadi 2021, which reports error counts against inconsistent and unlabelled denominators.

3.2. Characteristics of included studies

The 40 studies spanned 17 countries, the largest contributions from the USA (n = 11), the UK (n = 7), and Australia (n = 3), across intensive care, general wards, oncology, emergency, and outpatient settings. By design: 31 quasi-experimental (25 uncontrolled before-after, three with a concurrent comparison group not meeting the Tier 2 criterion, one interrupted time-series, one stepped-wedge, one segmented time-series), one concurrent-comparison cohort, two cross-sectional, three mixed-methods, and three qualitative.

One study used a concurrent-comparison cohort design (King 2003²⁰). Five studies that describe themselves as cohort or cross-sectional were reclassified as uncontrolled before-after on full-text review, because none has a concurrent comparison group: Potts 2004,²⁵ Satir 2023,²⁶ Jozefczyk 2013,²⁷ AlAzmi 2019²⁸ and Wimmer 2023.²¹ Full characteristics, with risk-of-bias judgements, are in Table 1.

3.3. Risk of bias

Risk of bias was assessed with the instrument matched to each design. Domain-level judgements for every study, with the reasoning behind each, are reported in Supplementary Table S3.

Under ROBINS-I, 27 of the 31 non-randomised intervention studies were at moderate risk of bias and four were at serious risk. No study was at low risk. This is a structural feature of the evidence base rather than a comment on how carefully individual studies were conducted. An uncontrolled before-after design has no concurrent comparison group and no modelling of the underlying trend. Bias due to confounding cannot be low, however well the study is executed. Following ROBINS-I, each study's overall judgement is its least favourable domain judgement.

The four serious ratings arise from two distinct sources. In two studies the comparator is the problem. AlAzmi 2019²⁸ compares a post-implementation sample against figures reported in separate earlier studies at the same hospital five years previously. Secular change and case-mix drift are left wholly uncontrolled. Kazemi 2011²⁹ does not account for prescriber experience or clinical-pharmacist presence on rounds, both plausible determinants of error rate. In the other two the problem is outcome ascertainment. Satir 2023²⁶ used retrospective chart review with raters unblinded to period, since the prescribing medium itself reveals allocation. Interrater agreement was only moderate on whether an error had occurred (Cohen's kappa 0.476) and slight on severity of harm (kappa 0.158). van Doormaal 2009³⁰ classified errors subjectively with unblinded observers.

That last rating warrants comment. Van Doormaal is one of the three Tier 1 designs, those that model the underlying trend. Design rigour and risk of bias are distinct axes. A design capable of separating the intervention from secular trend might still be executed in a way that admits substantial bias. A carefully conducted before-after study remains unable to make that separation at all. The two are reported separately throughout, and the design-rigour tiers used below are defined on design alone, not on appraisal outcome.

Of the remaining nine studies, the one concurrent-comparison cohort scored 7 stars on the Newcastle-Ottawa Scale (King 2003²⁰). The two cross-sectional process evaluations were appraised on MMAT rather than the Newcastle-Ottawa Scale, which is a cohort instrument: Hoonakker 2013³¹ is of high quality, while Hanauer 2013³² is of low quality, because its reporting checklist discloses that one observer conducted all pre-implementation sessions and a second all post-implementation sessions without calibration between them, so its before-after comparison is confounded with observer. On MMAT, two of the three mixed-methods studies were of high quality and one was low (Ayatollahi 2015,³³ effectively a single-strand quantitative survey). All three qualitative studies were of high quality on the JBI checklist. This raises rather than lowers confidence in the communication finding and supports the moderate CERQual rating assigned to it.

3.4. Medication error

Twenty-nine studies reported a medication-error outcome. Extracted results for each, including setting, decision-support status, denominators, study periods, pre- and post-implementation values, effect estimates and counter-findings, are given in Supplementary Table S7a.

At face value the evidence appears overwhelmingly positive. The large majority reported a reduction, ranging from a few percentage points to near-elimination: prescribing errors fell from 67.7 to 2.8 per 100 orders in Al-Sarawi 2019³⁴ and from 30.1% to 2.4% of medications in Hernandez 2015,³⁵ while the proportion of patients with at least one discharge prescribing error fell from 99.4% to 23.3% in Mills 2017,³⁶ which its authors report as 84% to 23% once omitted allergy information, made mandatory by the system, is excluded. This body of figures underlies the frequently cited range of roughly 20% to 98%.

3.4.1. Estimates that can be read against background change

Four studies report an estimate that can be read against background change rather than resting on a single before-and-after comparison: a modelled trend, a concurrent comparison group, a stepped-wedge rollout, or a multi-period series. In three of the four, the reduction in medication error is statistically supported.

Bates 1999³⁷ reported non-missed-dose errors falling from 142 to 26.6 per 1000 patient-days across four periods, an overall decline of 81% (p < 0.0001). The trajectory was not smooth. The rate fell 64% at period 1, rose 45% at period 2, then fell 64% again once the potassium ordering screens were redesigned. Non-intercepted serious errors fell 86% (p = 0.0003). The study has a single pre-implementation measurement, so it cannot estimate a background trend, and the 81% is the crude difference between the first and last periods. What the multi-period structure establishes is narrower: the rate moved with identifiable changes to the system rather than declining steadily, which a secular trend would not produce.

van Doormaal 2009³⁰ reported medication orders containing at least one error falling from 55% to 17%. Segmented regression attributed to the intervention an immediate absolute reduction of 40.3% (95% CI −45.13 to −35.48), together with a change in trend of −0.92% per week.

King 2003²⁰ found the medication-error rate 40% lower on the CPOE wards than on concurrent control wards (rate ratio 0.60, 95% CI 0.48 to 0.74), having first established that the wards were indistinguishable at baseline (0.93, 95% CI 0.76 to 1.13). On the authors' own arithmetic, 490 patient-days are required to see the benefit of one fewer medication error.

Franklin 2019³⁸ is the exception. Errors were found in 7.8% of paper orders and 6.0% of electronic orders, and three-level logistic regression showed no significant effect of electronic prescribing once clustering by patient and ward was taken into account (odds ratio 0.938, 95% CI 0.727 to 1.210, p = 0.621), and none of study week. Patient and ward both had significant effects, so the variation in this study is absorbed by where a patient was treated rather than by how the order was written.

3.4.2. What adjustment does to an estimate

Adjustment is often assumed to shrink an apparent benefit. It does not do so systematically. It removes whatever the underlying trend happens to be, and that trend might run in either direction.

van Doormaal 2009³⁰ shows both cases in the same data. Medication errors were rising before implementation, at 0.63% of orders per week (95% CI 0.35 to 0.91), so the adjusted immediate reduction of 40.3 percentage points is larger than the crude difference of 38 points. The authors call that rising baseline surprising and suggest it may itself be an artefact of the observers becoming better at detecting errors, since they were not blinded to period. Preventable adverse drug events were falling before implementation, at 4.04% per admission per month (95% CI −7.70 to −0.38), so the crude halving from 15.5% to 7.3% of admitted patients becomes an immediate change of −0.42% (95% CI −15.52 to 14.68), which is not significant. Two outcomes, recorded in the same patients over the same period, moved in opposite directions once the background was accounted for.

Urtasun 2022¹⁹ makes the same point without modelling. The children's hospital that implemented electronic prescribing fell from 29.1 to 19.9 prescribing errors per 100 prescriptions (OR 1.65, 95% CI 1.34 to 2.02, p < 0.01). The general hospital used as a concurrent control, which continued on a pre-designed structured paper form, fell from 24.9 to 13.6 (OR 2.1, 95% CI 1.5 to 2.8, p < 0.01). The comparison site improved by more. Read without its comparator, this study reports a significant 32% reduction and attributes it to electronic prescribing.

The implication for the 22 studies with neither a concurrent comparison group nor trend modelling21, 25, 26, 27, 28, 29, 34, 35, 36, 39, 40, 41, 42, 43, 44, 45, 46, 47, 48, 49, 50, 51 is narrower than it might first appear, but also harder to remedy. Their estimates are not necessarily inflated. The difficulty is that neither their magnitude nor their direction can be established. There was never a measurement of the trend against which they would have to be read. Cross-tabulation by design-rigour tier (Supplementary Table S2) shows reductions of 50% or more at every tier: two of the three Tier 1 designs, two of the three Tier 3 studies with a concurrent comparison, and 14 of the 22 uncontrolled studies. What separates the tiers is therefore not the size of the reported reduction but whether that reduction can be attributed to the intervention. The cross-tabulation describes how the evidence is distributed rather than demonstrating that the uncontrolled estimates are wrong.

3.4.3. Error substitution

Eight studies reporting headline reductions simultaneously documented error classes that their own authors attribute to the system: Satir 2023,²⁶ Mills 2017,³⁶ Sin 2021,⁴⁰ Kenawy 2019,⁴¹ Hodgkinson 2017,⁴⁴ Westbrook 2012,¹⁷ Hernandez 2015³⁵ and Bates 1999.³⁷ Two of the eight quantified how much of the residual error the system itself had produced. Hodgkinson 2017⁴⁴ identified 50 system-related prescribing errors, 68% of all prescribing errors recorded after implementation; 60% arose from new tasks the system required and 32% from limitations of the system itself. Legislative non-compliance rose from 0.2% to 3.3% of orders (p < 0.0001) and omitted liquid-dose calculations from 0.9% to 2.5% (p = 0.026). Clinical errors rose from 2.8% to 23% of all prescribing errors even as the total fell by 93%. Westbrook 2012¹⁷ found system-related errors in 34.8% of post-implementation errors (358 of 1029). Including them, the clinical error rate rose from 1.02 to 1.39 per admission; excluding them, it fell to 0.83 (p = 0.03). The authors conclude that system-related errors were a major reason the system delivered no significant reduction in clinical error.

The remaining six of the eight recur across settings and system types. In Bates 1999³⁷ intercepted potential adverse drug events rose to 59.4 per 1000 patient-days at period 2, 101 of the 106 being potassium chloride ordering errors that the system's initial ordering screen made easy to write; the rate fell to 0.5 once that screen was redesigned. These were errors intercepted before they reached a patient, counted here as an error class the system introduced rather than as harm; the realised adverse drug events reported in the same study are given in §3.5. Missed-dose errors also rose across the series, from 169 to 329 per 1000 patient-days (p < 0.0001), although the authors attribute that rise to pharmacy staffing and workflow changes rather than to the system. Duplicate-therapy prescribing rose from 0.4% to 1.8% in Hernandez 2015,³⁵ attributed by the authors to overlapping protocol orders. Omission and indication errors rose in Kenawy 2019,⁴¹ from 0.8% to 1.4% and from 1.8% to 2.9% respectively; the authors attribute the indication errors to menu selection, citing two drugs adjacent in the selection list. Mills 2017³⁶ recorded a new class the authors term sociotechnical, caused by the system, in eight patients. Sin 2021⁴⁰ eradicated handwriting errors but increased missing entry of patient information, which delayed dispensing. Patient-transfer errors, arising from prescriptions held simultaneously on paper and in the system, rose from 0.2 to 0.6 per 100 prescriptions among the potentially harmful errors in Satir 2023,²⁶ which also recorded a significant increase in the overall severity of harm. A further four studies recorded an increase in an error class without attributing it to the system. Hitti 2017⁴² recorded high-risk errors rising from 15.0% to 18.2% (p = 0.02) while low-risk missing-information errors fell from 59.1% to 35.5%, the authors attributing the pattern to the absence of decision support. Duplicate-therapy prescribing rose from 6% to 13% in Al-Sarawi 2019.³⁴ Duplication, omission and incorrect drug or formulation errors all increased in Franklin 2019,³⁸ whose authors point to screen design, citing a companion qualitative study, as a likely contributor to the duplication. Omission of the route of administration rose from 40 to 78 errors in Yugandhar 2017⁴³ against a larger post-period denominator.

Uncontrolled evaluations counting only the pre-specified error type cannot detect substitution of this kind. The two studies that did count it put the share high. In Hodgkinson two of every three errors left after implementation were errors the system itself had introduced, and in Westbrook one in three. In both, the net effect is materially smaller than the headline figure suggests. A related limitation applies where the reduction rests on error classes of limited clinical consequence: in Westbrook 2012¹⁷ procedural errors fell by more than 90% while clinical errors did not significantly change and rose in one intervention ward from 0.99 to 1.70 per admission, and in Jani 2008⁴⁸ the reduction is dominated by missing essential information, which fell from 73.3% to 1.4% of items, and by the elimination of illegibility.

3.4.4. Dependence on decision support

Benefit was repeatedly conditional on decision support rather than on order entry alone. In Kazemi 2011,²⁹ introducing CPOE without decision support produced no significant change in non-intercepted medication errors; only after dose and frequency support was added in the third period did the rate fall from approximately 53% to 34% (p < 0.001). Dosing-specific decision support drove the reductions in Hou 2013,⁴⁶ where initial dose errors fell from 2.25% to 0.91%, and in Cordero 2004.⁴⁵ Conversely, in Satir 2023,²⁶ where the system contained only interaction and duplication checks and no automated dose check, dosing errors did not change (5.6 versus 5.2 per 100 prescriptions, p = 0.555); the authors attribute this to a separate dosing-support application already in use before implementation. In Pontefract 2018,⁵¹ high-risk prescribing errors fell significantly at two of three sites and were unchanged at the third, with interruptive decision support having the greatest effect.

3.5. Adverse drug events

Seven studies reported an adverse-drug-event outcome. Extracted results are given in Supplementary Table S7b. Potential, preventable and actual events are reported separately there and are not aggregated. The distinction matters. A potential adverse drug event is an error with the capacity to injure that did not reach the patient or did not cause harm. A preventable adverse drug event is realised harm that need not have occurred. Only the second represents injury. Two further studies were considered for this panel and classified instead as medication-error evidence. Westbrook 2012¹⁷ graded prescribing errors on a five-point severity scale; a severity-graded process failure is not a realised event. Al-Sarawi 2019³⁴ reported the presence of adverse-drug-reaction alerts on the record, which measures documentation completeness rather than event incidence. Both are reported in Supplementary Table S7a.

None of the three designs capable of supporting a causal claim about harm demonstrated an effect: a controlled cohort, a four-period segmented time series and an interrupted time series. Two uncontrolled before-after studies that measured harm were also null. Bates 1999³⁷ reported total adverse drug events falling from 14.7 to 9.6 per 1000 patient-days across four periods (p = 0.09), with non-preventable events unchanged (p = 0.33) and preventable events rising in period 1, from 2.9 to 5.7 per 1000 patient-days, before falling. King 2003²⁰ found no effect (ratio of rate ratios 1.30, 95% CI 0.47 to 3.52) and its potential adverse drug events fell more on the control wards than on the intervention wards. Wimmer 2023²¹ found adverse drug events during hospitalisation in 2.7% of patients before and 2.8% after, a relative risk of 1.04 (95% CI 0.42 to 2.59); the interval spans a halving and a doubling, and the study was powered against an assumed event rate four times what it observed. Potential medication errors per patient fell from 1.69 to 0.71 (p < 0.01), while medication errors with relevant harm rose from 3.9% to 5.3% of patients (p = 0.390). Upperman 2005⁵² found no change in all adverse drug events (0.30 to 0.37 per 1000 doses, p = 0.3) and a borderline reduction in the harmful subset (0.05 to 0.03, p = 0.05). van Doormaal 2009³⁰ found no significant change after adjustment, as described above.

Holdsworth 2007⁵³ is the exception. Preventable adverse drug events fell from 46 to 26 and potential events from 94 to 35, across 1197 and 1210 admissions: relative risks of 0.56 (95% CI 0.34 to 0.91) and 0.37 (95% CI 0.25 to 0.55). This is a reduction in realised harm, not only in its opportunity. The design cannot carry the inference. The comparator is a dataset from an earlier study of the same care units, so the estimate absorbs whatever else changed between the two periods. This is the failure mode van Doormaal demonstrates directly, and the reason the claim here concerns what designs can support rather than what has been observed. Potts 2004²⁵ reported potential adverse drug events falling from 2.2 to 1.3 per 100 orders, a reduction of 40.9% as reported by the authors and markedly smaller than the 95.9% fall in all error types recorded in the same study. Westbrook 2012¹⁷ provides the one concurrent-controlled severity comparison: serious errors fell 44% in the intervention wards, from 0.25 to 0.14 per admission (p = 0.0002), against a non-significant 17% in the control wards (p = 0.40).

One study offers a mechanism for the divergence rather than only a statistical description of it. van Doormaal 2009³⁰ found an immediate reduction in every subtype of medication error except therapeutic errors, where the change was −0.91% (95% CI −2.37 to 0.56). The same authors had previously shown that therapeutic errors are the error type most strongly associated with preventable harm, and they suggest the null result on preventable adverse drug events may be explained by precisely this. The decision support in that study generated alerts only for overdosing, drug–drug interactions and allergies. On this reading the divergence between process and outcome is not merely a matter of statistical power: the errors that were prevented were largely those least likely to injure a patient, and the errors that injure patients were the ones the system did not address.

These findings might be interpreted with corresponding caution in the opposite direction. There is not much of an adverse-drug-event evidence base, and the event counts within it are smaller still. King 2003²⁰ recorded 18 events in total, and the interval around its null estimate runs from 0.47 to 3.52. Definitions of harm varied across studies, and follow-up was short relative to the time over which some medication-related harm becomes apparent. Absence of demonstrated benefit is therefore not evidence that no benefit exists. What can be said is narrower and more secure. The evidence establishes that electronic prescribing reduces the opportunity for harm. It does not establish that it reduces harm itself.

3.6. Workflow

Seven studies reported workflow outcomes, with genuinely mixed direction. Pharmacy-side workflow generally improved: faster verification and reduced clarification time (McMullen 2015⁵⁴; Chapman 2012⁵⁵). Prescriber-side task fragmentation fell in Hanauer 2013,³² where the average uninterrupted task lengthened from 131.2 to 218.3 s (p < 0.01) while ordering time did not fall (10.2% to 11.4% of clinical time); that study used different observers before and after implementation without calibration between them, and its authors note that a falling patient census may itself account for the reduced fragmentation. Prescriber-side workflow did not, with increased documentation time and workload (Armada 2014⁴⁹; Ayatollahi 2015³³). Gains in one step were frequently offset elsewhere, leaving overall task time often unchanged (Chapman 2012⁵⁵). Electronic prescribing redistributes workflow effort across professional groups rather than uniformly reducing it.

Two medication-error studies reported timing data that locate the asymmetry precisely. In Cordero 2004,⁴⁵ radiology order-to-arrival fell from 28 to 17 min (p < 0.001) while arrival-to-completion was unchanged at 14 against 15 min, giving an order-to-completion fall from 42 to 32 min: the gain is entirely in the ordering step, and the work of carrying out the order took as long as before. In Hodgkinson 2017,⁴⁴ median patient waiting time at dispensing fell 52%, from 27 to 13 min (p < 0.0001), attributed by the authors to fewer prescribing errors requiring resolution. Al-Sarawi 2019³⁴ shows the cost side: pharmacist annotations on medication orders fell from 19% to 5.1% (p < 0.0001) and documented pharmaceutical review from 38% to 26% (p = 0.0376).

3.7. Inter-professional communication

Seven studies, mainly qualitative and mixed-methods, addressed communication, with a consistently adverse short-term direction. The shift from synchronous, face-to-face to asynchronous electronic ordering reduced timeliness, openness, and contextual richness between prescribers and nurses, and reduced pharmacists' ward presence (Beuscart-Zéphir 2005⁵⁶; Pirnejad 2008⁵⁷; Mohsin-Shaikh 2023⁵⁸; McMullen 2015⁵⁴). Nurses were most consistently disadvantaged (Hoonakker 2013³¹; Ayatollahi 2015³³), although in Hoonakker the gap between nurses' and prescribers' ratings was already present before implementation. This rests on the strongest part of the qualitative evidence: all three qualitative studies were high quality, raising confidence. A workflow study bears on the same question: Kenawy 2019⁴¹ measured communication volume directly and found no change in telephone calls to prescribers (17.4% to 19.1%, p = 0.053) or in direct discussion with them (15.5% to 15.9%, p = 0.67) across five months either side of implementation, although pharmacy call-backs and patient returns to the prescriber both fell. Several studies documented recovery over time, suggesting the disruption is real but partly transitional. In Hoonakker 2013³¹ nurses' ratings fell at three months and returned to baseline levels or above at one year. The change across rounds was not statistically significant for nurses overall (p = 0.07), although communication timeliness was significantly lower at three months than at either baseline or one year, and the authors conclude that implementation had no negative long-term effect on communication quality.

3.8. Intervention-stratified observations

Stratifying by intervention sharpens the incremental value of decision support. Standalone CPOE/e-prescribing produced inconsistent error effects and sometimes none without CDSS (Kazemi 2011²⁹). The reductions in clinically meaningful errors and preventable ADEs were concentrated in studies of order entry paired with decision support (Bates 1999³⁷; Holdsworth 2007⁵³; van Doormaal 2009³⁰; Westbrook 2012¹⁷), including dosing-specific decision support (Hou 2013⁴⁶; Cordero 2004⁴⁵). Decision support was itself a source of new problems where alerting was excessive or low-value, contributing to alert fatigue and pharmacist work-shifting (Pontefract 201851, 59; McMullen 2015⁵⁴). Decision support is the component most associated with genuine benefit, but only when well-calibrated.

3.9. Certainty of evidence

Certainty was rated by outcome using GRADE and, for the qualitative communication finding, GRADE-CERQual. Ratings ranged from very low to moderate and are summarised, with the reasoning for each, in Supplementary Table S4.

4. Discussion

This review set out to examine whether the apparent benefit of electronic prescribing depends on the design of the studies that measure it. The answer is more specific than the question. Where the outcome is a count of medication errors, the reduction is large and holds in the studies best placed to test it. Bates 1999³⁷ reported 81% across four periods. van Doormaal 2009³⁰ reported an adjusted immediate reduction of 40.3 percentage points. King 2003²⁰ reported 40% against concurrent controls. Where the outcome is patient harm, no design capable of testing an effect has demonstrated one.

The divergence between the two is the central finding. Study design alone does not explain it. van Doormaal 2009³⁰ measured the pre-implementation trend for both outcomes. They ran in opposite directions: medication errors rising at 0.63% of orders per week, preventable adverse drug events falling at 4.04% per admission per month. Adjustment made the error estimate larger and the harm estimate null, in the same patients over the same period. What looked like a halving of preventable harm might simply have been the continuation of a decline already under way.

The same study offers a mechanism. Every subtype of medication error fell except therapeutic errors. The authors had previously shown that therapeutic errors are the type most strongly associated with preventable harm. Their decision support generated alerts only for overdosing, interactions and allergies. Satir 2023²⁶ points the same way: a system with interaction and duplication checking but no dose validation left dosing errors unchanged. What these systems reliably remove might therefore be administrative and procedural defects, while the clinical errors that injure patients could require decision support calibrated to them.

This has an implication for the wider literature. Twenty-two of the 29 studies reporting a medication-error outcome are uncontrolled before-after designs. These measure no background trend. Their estimates are not shown to be inflated. The difficulty is that neither direction nor magnitude can be established. Taken with the finding that reductions concentrate in error classes of limited clinical consequence, this might explain why the field reads more favourably than the outcomes justify. It aligns with the most methodologically careful prior syntheses, which found inconsistent effects on patient outcomes amid low-to-very-low-quality evidence⁹ and benefit confined largely to preventable rather than actual adverse drug events.¹⁰

Two further patterns support a cautious reading. Several studies reporting headline reductions also documented error substitution, with one error class eliminated as another emerged: potassium chloride ordering errors rose sharply in Bates 1999³⁷ until the ordering screen was redesigned, duplication and omission errors increased in Franklin 2019,³⁸ and patient-transfer errors arising from a hybrid paper and electronic system rose in Satir 2023,²⁶ which also recorded a significant increase in the overall severity of harm. Uncontrolled designs counting only the pre-specified error type are structurally blind to this, and the foundational cautionary literature remains pertinent: CPOE systems have been shown to facilitate novel error types through interface and information-fragmentation problems,6, 7 and rapid implementation has been associated with increased mortality.⁸

4.1. Implications

These findings do not imply that electronic prescribing is ineffective or should be deprioritised. The technology plausibly reduces the opportunity for prescribing error, and that is worth having. They do imply that its demonstrated value is narrower than the headline literature suggests, and that it lies in process rather than in outcome. Implementation decisions should be made on that more sober basis. Three practical points follow. Electronic prescribing should be deployed with well-calibrated decision support, not as order entry alone. Implementation should be accompanied by explicit surveillance for newly introduced error classes, namely duplication, omission, and selection errors, which conventional before-after evaluation will miss. The predictable short-term degradation of inter-professional communication, particularly for nursing staff, should be anticipated and actively managed. For evaluators and journals, the more durable implication concerns study design and outcome selection. The field has generated a large volume of uncontrolled before-after evidence that measures no background trend, and such evidence cannot establish the magnitude or even the direction of an effect. Future evaluations could privilege designs that measure the trend, namely interrupted time-series, stepped-wedge and controlled comparisons. They could also report harm and error substitution rather than error counts alone, since the error classes most readily prevented appear to be those least likely to injure a patient.

4.2. Strengths and limitations

The principal strength of this review is methodological. Rather than pooling a summary direction of effect, it separates the evidence on process failure from the evidence on realised harm and reads each against the designs capable of establishing it. It also reports design rigour and risk of bias as separate, non-derived attributes of every included study. This surfaces a divergence that conventional vote-counting and meta-analytic synthesis both obscure. The review also draws on a broad multi-database search and appraises each design with a fit-for-purpose instrument.13, 14, 15, 16 It reports the synthesis to a recognised standard for reviews without meta-analysis.²²

Several limitations apply. First, the absence of a pooled estimate reflects the genuine non-poolability of the reported metrics. This is appropriate, but the direction-of-effect coding that replaces it involves judgement. That judgement is made auditable through the effect-direction matrix and the detailed extraction table (Supplementary Tables S2 and S7). Second, publication bias is a live threat, although it bears differently on the two outcomes. Favourable uncontrolled before-after studies of medication error are more likely to be published, which would further skew an evidence base already dominated by such designs. On adverse drug events the bias runs the other way: null results are the less publishable finding, so the consistency of the null across every design able to test it is unlikely to be an artefact of selective reporting. There was no way to run a formal small-study test on non-poolable metrics. Third, the review was restricted to English-language studies published between 1994 and 2024, and the included evidence is concentrated in high-income settings. This limits generalisability to the low- and middle-income contexts where electronic prescribing is now expanding. Finally, the four domains were unevenly represented across studies. The communication and workflow evidence rests on a smaller number of high-quality qualitative and mixed-methods studies.

Two limitations concern the conduct of the review itself. First, PRISMA 2020 asks that a reason be given for each report excluded at full text. Reasons were recorded in the screening tool for 41 of the 71 reports excluded at this stage and were not recorded for the remaining 30. This requirement is therefore met only in part. The reasons that were captured are reported rather than a reconstructed complete breakdown. Second, eleven of the 130 reports advanced to full-text screening were not retrieved or not assessed. Reports were obtained through institutional subscriptions and open-access repositories; interlibrary loan was not pursued and authors were not contacted for reports that could not be obtained. At 8.5% of the reports sought, non-retrieval is unlikely to have materially altered the evidence base. The possibility that the unretrieved reports differ systematically from those assessed cannot be excluded.

5. Conclusion

Electronic prescribing reduces measured medication errors, and in three of the four studies whose design can read that reduction against background change it is statistically supported. In the fourth, a stepped-wedge design, it is not.

An effect on patient harm has not been demonstrated. The three designs capable of supporting a causal claim were all null: a controlled cohort, a four-period segmented time series and an interrupted time series. Where reductions in realised harm were shown, they rested on a comparison against a historical dataset from the same care units; the remaining reductions fell on potential events, which by definition did not injure anyone. The event counts are small enough that this is a statement about what the evidence establishes rather than about what is true.

The divergence has a plausible mechanism. In the one study to examine it, every subtype of error fell except therapeutic errors, which are the type most strongly associated with preventable harm and the type its decision support did not address. What these systems reliably remove are administrative and procedural defects. What injures patients appears to require decision support calibrated to the specific error.

Electronic prescribing also redistributes workflow effort across professional groups rather than reducing it, and disrupts inter-professional communication in the short term, with nurses most affected. Future evaluations could privilege designs that measure the background trend, namely interrupted time-series, stepped-wedge and controlled comparisons, and could report harm and error substitution rather than error counts alone.

Registration

PROSPERO CRD42024570480 (registered 7 October 2024).

CRediT authorship contribution statement

Sai Bhavana: Writing – original draft, Methodology, Investigation, Formal analysis, Data curation, Conceptualization. Sanjay Patil: Writing – review & editing, Methodology, Investigation, Formal analysis, Data curation. R.J. Varshini: Writing – review & editing, Methodology, Investigation, Formal analysis, Data curation. Edlin Glane Mathias: Writing – review & editing, Validation, Supervision, Methodology, Conceptualization. Rajesh Kamath: Writing – original draft, Validation, Supervision, Methodology, Conceptualization.

Ethics approval

Not applicable; this is a systematic review of published studies and involved no new human or animal participant data.

Funding

This research received no specific grant from any funding agency in the public, commercial, or not-for-profit sectors. No funding was received for the conduct of the research or the preparation of this article.

Declaration of competing interest

The authors declare that they have no known competing financial interests or personal relationships that could have appeared to influence the work reported in this paper.

Appendix A. Supplementary data

Supplementary material

Data availability

All data analysed are from the included published studies; the extraction dataset and risk-of-bias assessments are provided in the supplementary materials.