As potential patient samples we considered hospitalized children and adults of every age and indication, whose treatment involved the management strategy "clinical pathways". Given the problem that there are variations in the terminology used in the current research 13, we defined minimum "inclusion criteria" for meeting our clinical pathway definition (see Table 1). Based on our definition (see background), we developed a pre-specified, three operational pathway criteria as follows: 1) multidisciplinary (two or multiple clinical professions involved), 2) protocol or algorithm based (i.e. structured care plan/treatment-protocol or algorithm) and finally, 3) evidence based (pathway components were minimally based on one RCT or best practice guidelines). Every pathway characteristic could be met as (1) "yes" criterion; (2) "not sure" because of poor reporting and the failure to contact the principal author or (3) "criterion not met." If one or more pathway criteria selected is not met, then we excluded the study.

Please note, additional information relating to the included studies that matched these requirements or differ from each other, are given in the results section of this review.

The setting definition covered the whole range of services offered by the clinical (out- and in-patient) as well as in the in-patient rehabilitation sector. We only gathered robust evidence and limited our study selection to randomised controlled trials (RCT) and controlled clinical trials (CCT) including methodological quality criteria (please see "quality assessment and data analyses").

We considered every objective economic and patient outcome for inclusion. We pre-defined (1) in-hospital complications as a secondary disease or adverse medical occurrence during hospitalization 14 and (2) we defined re-hospitalization as a readmission within a specified follow up period of an index admission.

We performed specialised searches of the Medline database (1966–2006), Embase (1980–2006), Cinahl (1982–2006), Global Health (1973–2006), and the specialised Cochrane register (including NHS EED and HTA Database; last update: 13.11.06), not restricted by language or country. We used free text words (tw), medical subject headings (MeSH terms -/-) or exploded MeSH terms for our MEDLINE literature search. This controlled vocabulary was adapted (as much as possible) to the indexation (thesaurus) of all other databases included in this review. We demonstrate our "clinical pathway search strategy" with the MEDLINE inquiry (Table 2).

Furthermore, we employed citation tracking, which examines included studies and previous reviews and contacted investigators to identify any study missed by the electronic searches.

For quality of studies (see additional File 1), we adhered to the Effective Organisation of Care Group (EPOC) module15 and defined three risk classes: Class I (low risk of bias), Class II (moderate risk of bias) and Class III (high risk of bias). Two reviewers independently assessed and abstracted data, on the intervention criteria, study characteristics and methodological quality. Any disagreement was discussed with a third reviewer. Studies with a high risk of bias were excluded from the review after documentation. If a primary study did not provide information about the standard deviation, we used the approximative or direct algebraic connection between the stated confidence intervals, or p-values, and the standard deviation and calculated the inverse transformation to the individual or pooled standard deviation 12. Prior to the actual statistical pooling of the singular effects, an adjustment of the data regarding costs due to inflation and price adjustment (OECD Health Care Price Index) was carried out 16. We chose the US Dollar (USD) as the basic currency. The year 2000 was chosen as a representative year for inflation and price adjustments or exchange rates.

We used Review Manager (RevMan) of the Cochrane Collaboration to calculate a pooled effect estimate, called weighted mean difference (WMD) 17. We used a random effects model since this model estimates the effect with consideration to the variance between studies, rather than ignoring heterogeneity by employing a fixed effect model. The effect sizes were generated using a model fitting inverse variance weights 17.

Despite the expected clinical heterogeneity (clinical variability of the included pathway interventions) within the review, it is important to assess the comparability of the results from individual studies. A useful statistic for quantifying inconsistency is I² = [(Q df)/Q] × 100%, where Q is the chi-squared statistic and df is its degrees of freedom 12. This quantifies the total variance explained by the heterogeneity as a percentage. We considered an overall test-value greater than 60% to serve as evidence of substantial heterogeneity of a magnitude were statistical pooling is not appropriate.

In a sensitivity analysis, both fixed effects and random effects models were employed to determine the causes of heterogeneity and test the confidence that can be placed in both estimates. Only robust estimations of the pooled effects with similar results in fixed effects and random effects models are included in the meta-analysis and discussed. Furthermore, sensitivity analyses were performed to test whether the effect size varied by the countries where the study was carried out (adjusting for market forces) and the year of publication, adjusting for temporal trends.

We decided previously to perform a subgroup analysis of invasive versus non-invasive clinical pathways, whereupon the distinction between invasive or non-invasive interventions refers to the nature of patient management guided by clinical pathways (i.e. clinical pathways for gastrectomy; transurethral resection of the prostate; hip and knee arthroplasty; percutaneous transluminal coronary angioplasty; etc. versus clinical pathways for asthma care; stroke; pneumonia; etc.). According to theories on health economics, invasive procedures can be standardized more easily than treatment strategies in conservative sectors due to the lower treatment variance 18.

We used a funnel plot analysis to assess publication bias, i.e. the bias caused by a lower likelihood of publication for non-significant studies. The funnel plot is a scatter-plot with the x-axis representing the effects estimated from the primary studies, and the y-axis representing a measure of the sample size in each study (SE; standard error of the mean) 19. If publication bias is absent, the diagram shows an inverted symmetrical funnel.

However, given that publication bias poses a threat to the validity of this meta-analysis and the graphical method is subjective in nature, we also applied a statistical approach, often called fail-safe N test.

This test provides an estimate of the number of unpublished or in this context called file-draw studies (Nfs) having an average of no effect that is necessary in the analysis for reducing the pooled effect size from significant to non-significant 20. Using a critical d level (d crit) of -0.20, the estimate of unpublished studies was calculated with

Nfs = (Ntotal (mean d - d crit))/d crit;

where Ntotal is the total number of studies included in the Meta-Analysis and d is the overall pooled effect (WMD).

The distribution of the length of stay is limited downwards in a natural way (because of the minimum value is always 0), whereas upwards the values can scatter significantly. According to logarithmic transformation, values with this characteristic can have an approximately normal distribution 21. In the additional File 2 we detailed the formulas used for log transformation. Data analyses were performed using SPSS version 15.0 22.

The specialised search strategy led to the initial selection of 2,386 studies, whereas only 17 matched our methodical requirements (see Figure 1 &2). For the first stage of the study assessment, we scanned all of the 2,386 titles and abstracts for inclusion, the remaining 256 possibly relevant studies were retrieved as full text articles. Based on the full text assessment, we excluded 190 studies out of 256 because they failed to meet our pathway definition. The majority of the excluded studies failed to meet the multidisciplinary pathway criterion, i.e. it was a therapy guideline issued by a medical association or it was a uni-professional nursing care plan. Others did not meet the "algorithm or protocol based" criterion because there was no structure and detailed care plan. For example a poster with issued guidelines was posted in the Emergency Department.

Evidence for meeting the minimal criterion "pathway content is minimally based on one RCT" was reported in 15 studies out of 17, which were included in the review. The study from Falconer et al. and Swanson at al. met the evidence criterion, "not sure" because we failed in contacting the principal investigators 2324.

The reported pathway strategies can be described as complex pathway interventions versus a "non-intervention" control group or often poorly, described as "usual or traditional care" group. Most of the experimental interventions were combined with other types of interventions like audit and feedback, educational meetings, and reminders. For 8 out of the 17 (47%) included studies, it was clear that the structured care plan was combined with a "clinical diagnostic or assessment protocol"2325262728293031.

The evidence base for two (12%) pathway interventions was "not sure," whereas the remaining 15 interventions were minimally based on one randomized study or good evidence. The reported purpose of the pathway strategies was appropriate management or cost containment.

The hospital setting was in two studies a multi-center study comprising a range of hospitals included in the investigation 2630. From the 15 remaining single center studies, 8 studies (53%) were carried out in a university (teaching) hospital setting 2427282932333435 and 7 studies (46%) in a non-university hospital setting 23253136373839.

Details of the intervention characteristics are given in Table 3.

To summarize, we examined the design and study quality of 66 studies, excluding 49 out of the 66 studies because of the high risk of bias (see trail flow, Figure 1). Characteristics (reason for exclusion: see additional File 3) of the 49 excluded studies (references to excluded studies: see additional File 4) are given in detail.

The patient was randomized to the experimental or control group in 12 out of 13 (92%) RCTs. The randomization process was clear in all such studies and justified by the authors. Referring to the individually randomized and single-center studies, the assessment of protection against contamination of the control professionals remained unclear due to poor reporting. None of the investigators reported protection against contamination (communication between experimental and control professionals) and it is possible that control subjects received the intervention. Only the investigation from Marie et al. used a robust cluster randomized design, with 19 hospitals as unit of allocation 30. To avoid "unit of analysis error," we conducted the meta-analysis at the same level as the allocation (19 cluster-hospitals = 19 patients).

Poor reporting also lead to difficulties in determining the assessment of the power calculations. For instance, sample-size calculation was unclear for over 60% of the included studies; hence the study sample may not have been sufficiently large. Another problem, due to poor reporting was the selection of comparators. The choice of the comparator (i.e. the control and intervention units were located either in the main building or the east building of the participating hospital) was stated and justified by the authors of the 17 primary studies. However, a clear description of what was meant by traditional care or usual care (control group) would have helped in assessing the relevance of the study to other settings.

Primary studies reporting economic data, can be described by a very limited scope of evaluation, focusing on direct hospital LOS and costs effects, rather than on a full economic evaluation 16. In Table 3 the quality assessment and characteristics of the 17 studies included in the review and meta-analysis are shown in detail.

Out of the 16 studies (12 randomized and four non-randomized studies representing a study population of 4,028 patients) examining the effect of clinical pathways on the length of stay, 12 showed significant effects 23242627282930313233343536373839. However, heterogeneity between studies reporting on LOS was substantial (I² = 80%) and may refer to both the statistical inconsistency as well as to the varying clinical pathway interventions that were included. As a result, the estimation of an overall pooled effect is not appropriate and in Figure 3, the differences from the individual studies in LOS are depicted together with the corresponding confidence intervals without totals. The reported LOS in Kiyama 2003 was calculated from the day of surgery to the day of discharge 39. All other studies included in this analysis considered the total LOS.

Out of 17 trials reporting effects on quality outcome measures (see Table 1); six measures were comparable in terms of re-hospitalisation and seven in terms of in-hospital complications 23242526272829303132333435373839. In total, nine primary studies were included in the Meta-analysis (representing a study population of 1,674 patients), examining the effect of clinical pathways on quality patient outcomes. The pooled Odds Ratio (OR) for re-admission was 1.1 (95% CI: 0.57 to 2.08) and for in-hospital complications the overall OR was 0.7 (95% CI: 0.49 to 1.0). Statistical heterogeneity was not present among the studies and there was no evidence of difference in readmission to hospitals or in-hospital complications. The effects of clinical pathways on clinical outcomes in the individual studies are depicted together with the pooled OR (see Figure 4 &5). There was clinical variance in the range of follow-up periods that were used by the investigators measuring re-hospitalization (follow up periods ranged from 27 days to 6 month, see Table 1) as well as the investigators used varying definitions of the term in-hospital complications (included in-hospital complications were cardiac events, infections, thrombosis, re-operation, sepsis and empyema). Obviously, this implies that any time element in the patient outcome data is lost through this approach and it was not possible to compute a series of dichotomous outcomes, i.e. at least one event during the first year of follow up.

Six of the included studies (five randomized and one non-randomized), representing a sample of 1328 treated patients, reported on cost effects 262831333439. Four out of the five randomized studies found significantly lower hospitalisation costs for pathway groups. The statistical heterogeneity was substantial (I² = 88%) and compromised the estimation of a pooled effect. Additionally, we also observed a considerable methodological variation which refers to the different methods of cost calculation used by the investigators. Some investigators used a full cost approach (fix and variable costs included), whereas others calculated only direct hospital costs. Table 4 describes the costs differences in detail.

Five of the randomized studies, and two further non-randomized studies assessed the LOS effects of surgical or minimally invasive interventions 24262729353739. The pooled effect for all invasive primary studies was -2.5 days (95% CI: -3.53 to -1.41). The differences in LOS in the individual studies are depicted together with the total effect per study type (RCTs versus CCTs, Figure 6). The statistical pooling of the subgroup of surgical pathway interventions is characterized by a considerable overall test-value for statistical inconsistency (I² = 60.9%) which also reflects the clinical heterogeneity of the surgical pathway interventions included in this comparison.

The subgroup of the conservative pathway indications 232830313233343638 had a reduction of LOS of approximately one day (WMD -0.75; 95% CI: -1.23 to -0.27, Figure 7).

The LOS effects were robust in terms of the sensitivity analysis concerning the different statistical calculation models (fixed versus random effects model) and the Year of publication, adjusting for temporal trends. However, we observed a trend toward greater reported LOS effects from Japanese studies with a reduction of approximately three days (WMD – 2.7), followed by studies carried out in Australia (WMD – 1.5), Canada (WMD – 1.4) and the USA (WMD – 0.8). Subsequently, we tested the hypotheses, that different market forces (reported effect sizes per country) are possibly confounding the conclusions of these review and meta-analysis. After exclusion (stepwise/iterative and all of the primary Japanese studies) of the subgroup of Japanese studies, the (calculative) overall LOS effect remained robust and statistically significant, but tended to be smaller (WMD – 1.2; subgroup "Japanese studies excluded" versus WMD – 1.5; subgroup "all primary studies" included). This applies also to the subgroup Analysis "Invasive versus non-invasive LOS effects", after exclusion of the subgroup of Japanese studies (WMD -0.6 conservative versus -2.2 invasive).

In addition, the overall odds ratios (OR) for re-admission and in-hospital complications were robust in all terms of the sensitivity analysis, indicating reliable pooled results.

The funnel plot showed a relatively symmetric distribution (Figure 8), but the point cloud does not have a distinctive funnel form. The deficient funnel form of the funnel plot can also be due to the relatively high heterogeneity with respect to the different pathway indications of the primary studies included in these review (cross-indicational methodology of the primary studies). Furthermore, the number of studies was relatively small. However, given that publication bias may still exist, the statistical fail-safe N objectively helps to quantify. The calculation about the number of file-drawer studies showed that 101 non-significant studies would have to exist to reduce the (calculative) overall effect size of (WMD) – 1.47 to a mean effect size of – 0.2. These results indicate that unpublished research is unlikely to threaten the validity of the original meta-analysis.

The graphic distribution of the original and the logarithmical (natural logarithm LN) LOS data clearly indicates that there is a significant deviation from the normal distribution (Figure 9a &9b). The heterogeneity between studies was not substantially lowered by the log transformation.

The LOS reduction was estimated as 25 percent (95% CI: -36% to -14%). For example, with the average length of stay of 7 days, the estimated LOS effect was approximately -1.7 days (7 days * -0.25 = -1.75 days LOS reduction). Furthermore, the pooled percentage LOS effects were similar in fixed versus random effects models (WMD -0.25 versus WMD -0.21).