Enhanced care by generalists for functional somatic symptoms and disorders in primary care
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
This review aims to evaluate the clinical effectiveness of enhanced care interventions for FSS by primary care professionals. The review focuses on patient outcomes.
Background
Description of the condition
Patients with physical symptoms which cannot be explained by pathologically defined disease are common in primary care (Fink 1999a; Kroenke 1989; Peveler 1997; Toft 2005; Verhaak 2006). They represent a spectrum of conditions ranging from mild self‐limiting symptoms to severe and disabling disorders (Katon 1991; Rosendal 2007). As the number and severity of symptoms increases, so does the disability and the prevalence of psychological distress and dysfunctional illness cognitions (Hansen 2007; Kroenke 1994); there is good epidemiological evidence that the physical and psychological processes are inter‐related (Aggarwal 2006; Hotopf 1998).
For the purposes of this review, the term Functional Somatic Symptoms (FSS) is used to refer to the presence of physical symptoms that are not attributable to organ pathology or any conventionally defined disease and which meet additional criteria such as the number of symptoms or other clinical characteristics. This term is used in preference to the alternative term of Medically Unexplained Symptoms (MUS). Patients with severe FSS have impaired health related quality of life (Gureje 1997; Smith 1986), disproportionate healthcare costs (Barsky 2001; Fink 1999a; Smith 1986) and lower satisfaction with their healthcare providers (Frostholm 2005; Lin 1991).
There is no universally agreed way of classifying FSS (Sharpe 2006). FSS includes functional somatic syndromes: clusters of related symptoms which are typically specific to one organ system or medical speciality. Some of the best known are irritable bowel syndrome, fibromyalgia and chronic fatigue syndrome. At least 29 such syndromes have been described (Henningsen 2007); new syndrome definitions continue to appear and old ones to evolve. Importantly, there is substantial overlap between syndromes (Deary 1999; Wessely 1999) and most adult patients with FSS, regardless of which symptoms they present, experience symptoms in a range of bodily systems (Fink 2007). Psychiatric classifications typically view individuals on a spectrum of severity from the most severe, Somatisation Disorder, through to the mildest abridged somatisation (Escobar 1989). Some patients on the FSS spectrum will also demonstrate pathological health anxiety or hypochondriasis (Francis 1994; World Health Organisation 1993). While many patients with FSS meet criteria for co‐morbid anxiety or depressive disorders, these are not invariably present and the concept that FSS might simply represent somatised psychiatric illness is not tenable.
The prevalence of FSS in primary care depends on the sampling strategy and the definitions used. Studies of the reason for consulting find that approximately 15% of patients seeing their GP do so for a symptom not obviously explained by organic disease (Peveler 1997; Rosendal 2003), but the proportion consulting repeatedly for an unexplained symptom is considerably lower (Verhaak 2006). 20‐30% of GP consulters aged 18‐65 meet criteria for somatoform disorders (Arnold 2006; Fink 1999a; Toft 2005) but not all will present unexplained symptoms at that consultation. Less than 1% of GP consulters have the most severe Somatisation Disorder (Fink 1999a; Toft 2005). The natural history of FSS varies between individuals and symptom patterns frequently change over time. Overall approximately half of patients with FSS will improve spontaneously over a year (Barsky 1998; Craig 1993; Gureje 1999; Lieb 2002 ).
Description of the intervention
Methods of treating FSS
Historically, attempts to treat FSS have used a psychosomatic perspective, whereby physical symptoms are thought to arise from (hidden) mental distress. Mind‐body interactions are now seen as more complex but can be usefully viewed within a cognitive‐behavioural model. This perspective has led to effective treatment by specialists for somatoform disorders (Kroenke 2000) and some specific syndromes (Henningsen 2007). An evolving family of brief therapies for primary care, originally termed "reattribution" (Goldberg 1989) has been developed for use in primary care; such therapies have features in common with the more detailed cognitive behavioural models. The original reattribution model targeted psychiatric illness, i.e. presenting somatisation (Goldberg 1989) and was built on problem‐solving therapy. Later the model was extended by Gask and Morriss to a wider range of somatisation processes (Morriss 2006). A recent extended reattribution model integrated elements from cognitive therapy such as "reframing" in a way which integrated mind and body using a descriptive approach to FSS rather than implying causation (Fink 2002).
Enhanced care
'Enhanced care' is defined as the use of a structured treatment model which draws on explanations for symptoms in broad bio‐psycho‐social terms and, or, encourages patients to develop additional strategies for dealing with their physical symptoms. It includes “reattribution” (Goldberg 1989) and “reframing” (Fink 2002) models. Treatment is delivered by primary care clinicians to their own patients after the training of these physicians in the enhanced care model. Primary care clinicians include doctors and other health care professionals providing first contact care across a wide range of clinical domains (Boerma 1999; Starfield 1994; World Health Organisation 2001). Typically, training will involve experienced primary care clinicians taking time from their routine work and being taught both a theoretical framework and practical techniques to use within consultations with their own patients. Following the training, additional time for longer consultations may, or may not, be made available for the trained clinicians.
How the intervention might work
Early studies of reattribution training in primary care used a before‐and‐after evaluation with no randomisation. They showed that GP’s skills were improved (Kaaya 1992) in a way which improved patient wellbeing (Morriss 1999) and reduced healthcare costs (Morriss 1998), these findings were taken to support the notion that making the link between psychological distress and physical symptoms led to better outcomes.
Subsequent studies have suggested various additional mechanisms, including providing extra time for patients, allowing expression of emotions or building useful explanations (Brody 1990; Dowrick 2004; Salmon 2007). Given that FSS is an umbrella term for a heterogeneous group of patients and disorders, it is likely that different psychological and physiological processes will be relevant for different individuals. It is also plausible that paradoxical effects of psycho‐social intervention will be seen whereby some patients benefit while others become more distressed, at least in the short term. There is some epidemiological (Kirmayer 1991) experimental (Graugaard 2003) and interventional (Schweickhardt 2005) evidence to support this conjecture.
Given the variety of patient groups, psychological processes and physical symptoms we consider enhanced care as a complex intervention Campbell 2001.
Why it is important to do this review
We are currently aware of several studies which have evaluated enhanced care models, partially or fully based on reattribution, for patients with FSS. While these have shown positive effects on GP’s attitude (Rosendal 2005) and diagnostic awareness (Rosendal 2003), effects on patient outcomes have been modest and insignificant in individual trials. We wish to carry out a systematic review and meta‐analysis of the clinical effectiveness of these interventions.
This review fits alongside another Cochrane review, 'Patient consultation letters for medically unexplained symptoms' (Hoedeman 2008) which involves specialist assessment of individual patients. This review includes some studies in the broader review of psychosocial interventions delivered by general practitioners (Huibers 2007) but we focus only on FSS and include more recent studies .
Objectives
This review aims to evaluate the clinical effectiveness of enhanced care interventions for FSS by primary care professionals. The review focuses on patient outcomes.
Methods
Criteria for considering studies for this review
Types of studies
All randomised controlled trials of enhanced care compared against treatment as usual.
Studies will be restricted to the primary care setting and to treatment models which are specific to that setting. Studies of specialist interventions hosted in primary care (for example prolonged contact with a psychotherapy specialist at the primary care clinic rather than hospital) will not be included.
Studies will be included without regard to the unit of randomisation, i.e. whether individual clinicians or clusters of clinicians are randomised. Crossover studies will not be included because the nature of the intervention ‐ a change in practice ‐ permits crossing over in one direction only.
Types of participants
Clinicians
Studies will be restricted to those in which treatment is delivered by generalists such as general practitioners, nurse practitioners or other health care professionals working within the primary care setting with first contact and ongoing care for patients regardless of their presenting problems. This excludes care provided by mental health professionals. No exclusions will be made on the basis of age, years of practice, practice type, and previous psychological training.
Studies must include specific training of participating clinicians; in groups where practitioners work together, this may be either to individuals or to the whole group.
Patients
Studies will be limited to those involving adults (at least 18 years old) with FSS, identified either by case finding or by the primary care clinician’s assessment of the presenting problem. In the absence of universally agreed criteria for FSS, studies in which patients are included based on their clinician's own assessment of the presenting problem as “medically unexplained” will be included. Case finding studies will be required to use validated instruments for FSS such as rating scales and interviews (Table 1). Studies of a single functional syndrome (e.g. Irritable Bowel Syndrome) will be included provided they meet the other criteria.
| Type of instrument | Name | references |
| Questionnaire | Abridged criteria | |
|
| PHQ‐15 | |
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| SCL‐som | |
|
| Whiteley‐7 | |
| Interview | SCAN | |
|
| DIS | |
|
| CIDI | |
| Health care use | Frequent attendance |
The table may be supplemented by specific instruments for functional somatic syndromes
The final review will also include a table of names and classification terms
Studies where the primary entry criterion is a specific non‐somatoform mental health disorder (e.g, depression, anxiety, post‐traumatic stress disorder) will be excluded. However, the presence, or continuing treatment, of one or more common mental disorders such as depression and anxiety in patients included with FSS will not lead to automatic exclusion. Our definition of FSS excludes factitious disorder and psychiatric illness arising as a complication of an organic disease (for example depression in a patient with heart disease).
Types of interventions
Experimental condition
Studies will be included if they employ a model of enhanced care, based on reattribution or reframing of symptoms, characterised by psychosomatic explanations for physical symptoms and “making the link” between symptoms and mental distress. The intervention must be delivered by either a generalist after additional training or a generalist acting as an intermediate specialist such as a general practitioner with a specific interest. Delivery may be provided either within routine consultations or during additional dedicated appointments which may be longer than usual or involve specific reimbursement.
The duration, content and degree of formalisation (eg written manual) of the training will be described for studies but we will not specify criteria in advance as different methods may be applicable in different professional cultures. Studies will be restricted to the primary care setting and to treatment models which are specific to that setting. Studies of specialist interventions hosted in primary care (for example prolonged contact with a psychotherapy specialist at the primary care clinic rather than hospital) will not be included.
The review does not include organisational changes involving shared care models with mental health professionals (Cochrane consultation letter review (Hoedeman 2008)). Trials of pharmacological treatment will be excluded but pharmaceutical treatment is permitted as part of the general treatment.
Control comparators
Studies for inclusion should have, as a control comparison group, patients receiving treatment as usual.
Types of outcome measures
Primary outcomes
The primary outcome measure is patient health status measured by a validated quality of life tool. Specifically, for SF‐36 and related tools (SF‐12, SF‐8) the primary outcome will be the physical and mental component summary scores.
Secondary outcomes
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Measures of symptom load (number and/or severity of symptoms), for instance using a checklist such as PHQ‐15 (Kroenke 2002) or Somatic Symptom Index. While symptoms are likely to be related to health related quality of life, the number and intrusiveness of symptoms appears to be a central characteristic of FSS.
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The patients’ illness beliefs, using a validated tool such as the Illness Perception Questionnaire Weinman 1996
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Depression and anxiety measured by questionnaire (eg Hospital Anxiety & Depression Scale)
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Functional status measured as sick leave
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Patient satisfaction with care
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Health care utilisation: The review will analyse medical consumption if stated outcomes can be compared either as number of visits and days in care or as health care costs
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Attrition from studies
We will analyse both primary and secondary outcomes as continuous measures and will test for positive and negative treatment effects in by looking for changes in measures.
Outcomes will be categorised as short term (0‐5 months), medium term (6‐11 months) or long term follow‐up (12 or more months). The primary focus will be on 12 month follow‐up data where available.
Search methods for identification of studies
Search of literature will be limited to the time period 1966 to publication of this review.
No language restriction will be employed.
Electronic searches
We will use a broad search strategy for Functional Somatic Symptoms (FSS) but limit the search to RCTs and primary care.
Searches will be conducted in: The CCDAN specialised registers (CCDANCTR‐Studies and CCDANCTR‐References, Appendix 1), the Cochrane Central Register of Controlled Trials (CENTRAL), the Database of Abstracts of Reviews of Effectiveness (DARE), Medline (1950‐) (Appendix 2), Embase (1980‐), PsychINFO (1806‐), CINAHL (1982‐), PSYNDEX, SIGLE, and LILACS.
All reference lists of relevant papers will be screened and author names from identified studies will be searched electronically.
Searching other resources
The electronic searches will be supplemented by hand searches in:
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Conference proceedings: International Psychosomatic Research, European liaison‐psychiatry and the Academy of Psychosomatic Medicine.
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Reference lists of retrieved and potentially relevant papers, as well as relevant systematic reviews, dissertations, theses and literature reviews.
Furthermore, we will contact first authors of identified studies and other experts in the field for information about published or unpublished studies (this includes contact to research groups that have been taught reattribution by Linda Gask).
Data collection and analysis
Selection of studies
MR and CB will independently screen all study abstracts identified by the search strategy. When there are disagreements about the selection of a trial a third review author (MS or KK) will be asked to assess the trial and the evaluation by MR and CB. In view of the relatively small field of interest and the involvement in the review of several trial investigators, we believe that blinding of review authors is not possible.
Data extraction and management
The study characteristics of selected trials will be extracted by two of three review authors (MR, CB, NB) thereby avoiding investigators reviewing their own studies. The extraction will be conducted independently by two authors. Disagreements between the authors will be resolved by discussion with a third author (PF). The provisional data extraction form is presented in Table 2 and will be pilot tested by MR and CB on five studies before implementation.
| Rubric | Reviewer 1 | Reviewer 2 | Conclusion | |
| Author name |
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| Title of paper |
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| Name of study |
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| Personal notes (e.g. name of disorder used) |
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| Reason for exclusion |
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| Study characteristics |
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| Assessment of methods (table 2) |
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| Setting of the study (the primary care organisation) |
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| Level of randomisation and measures of clustering |
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| The risk of contamination (control patients receiving intervention unintentional or vice versa) |
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| Doctor characteristics and sampling (previous training, years in practice, GP age) |
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| Patient characteristics (inclusion, exclusion, ethnicity, diagnosis, symptom duration, psychiatric co‐morbidity) and sampling (population screening, waiting room screening, GP assessment, diagnostic instruments used) |
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| Intervention* in active group |
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| Intervention in control group |
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| Outcome measure and instrument for assessment (primary outcome, secondary outcome, subgroups) |
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| Length of maximum follow‐up |
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| Results |
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* Interventions
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Training (duration, content, skills training, supervision)
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Treatment model: reattribution and how close it is to the original, psychosocial interventions other than reattribution). To which degree does the model for patients stipulate that physical symptoms are secondary to psychosocial distress.
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Clinicians (GP, nurse, other)
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Organisation (flagging of patients, consultation duration, number of consultations, no changes)
Assessment of risk of bias in included studies
We will assess the risk of bias using the Cochrane Collaboration’s tool for assessing risk of bias and report the results in a standard Risk of Bias table assessing the following domains
1) Sequence generation: Was the allocation sequence adequately generated?
2) Allocation concealment: Was allocation adequately concealed?
3) Blinding of participants, personnel and outcome assessors for each main outcome or class of outcomes: Was knowledge of the allocated intervention adequately prevented during the study?
4) Incomplete outcome data for each main outcome or class of outcomes: Were incomplete outcome data adequately addressed?
5) Selective outcome reporting: Are reports of the study free of suggestion of selective outcome reporting?
6) Other sources of bias: Was the study apparently free of other problems that could put it at a high risk of bias?
A description of what was reported to have happened in each study will be provided, and a judgement on the risk of bias will be made for each domain within and across studies, based on the following three categories:
A. Yes (low risk of bias)
B. Unclear
C. No (high risk of bias).
The study quality will be assessed by two reviewers independently (MR, CB, NB) and disagreements will be resolved by consulting MS or KK. Where necessary, the authors of the studies will be contacted for further information. The primary analysis will include all studies. A secondary sensitivity analysis will be conducted including only studies rated as at low to moderate risk of bias.
Measures of treatment effect
Continuous outcomes: where the patient populations are comparable but outcome measures vary between studies, effect sizes will be extracted as standardised mean difference (SMD) with 95% confidence intervals from continuous measures.
Dichotomous outcomes: these outcomes will be analysed by calculating a pooled relative risk (RR) for each comparison, with 95% confidence intervals. Where overall results are significant, the number‐needed‐to‐treat (NNT) to produce one outcome will be calculated.
Unit of analysis issues
As these are studies of interventions at the GP level, but with outcomes at the patient level, cluster effects are possible and should ideally be addressed in the study design. For trials which do not use a cluster randomised design we will carry out an adjustment to effective sample size. For this, we will attempt to derive an intra‐cluster correlation coefficient from other studies within the review, or failing this assume an intra‐cluster correlation of 0.05 based on the finding that the intra‐cluster correlation is typically lower than 0.05 for outcome variables in primary care (Campbell 2001).
Studies with different clinical entry criteria or diagnostic groups will all be included in the same analysis rather than carrying out separate analyses.
Dealing with missing data
In the first instance we will approach original authors to obtain missing data. If this is not available then missing dichotomous data will be managed through intention to treat (ITT) analysis, in which it will be assumed that patients who dropped out after randomisation had a negative outcome. Best / worse case scenarios will also calculated for the clinical response outcome, in which it will be assumed that dropouts in the active treatment group had positive outcomes and those in the control group had negative outcomes (best case scenario), and that dropouts in the active treatment group had negative outcomes and those in the control group had positive outcomes (worst case scenario), thus providing boundaries for the observed treatment effect.
Missing continuous data will either analysed on an endpoint basis, including only participants with a final assessment, or analysed using last observation carried forward to the final assessment (LOCF) if LOCF data were reported by the trial authors. Where SDs are missing, attempts will be made to obtain these data through contacting trial authors. Where SDs are not available from trial authors, they will be calculated from t‐values, confidence intervals or standard errors, where reported in articles (Deeks 2007a; Deeks 2007b). If these additional figures are not available or obtainable, the study data will not be included in the comparison of interest.
Assessment of heterogeneity
Statistical heterogeneity will be formally tested using the natural approximate chi‐square test, which provides evidence of variation in effect estimates beyond that of chance. Since the chi‐squared test has low power to assess heterogeneity where a small number of participants or trials are included, the p‐value will be conservatively set at 0.1. Heterogeneity will also be tested using the I2 statistic, which calculates the percentage of variability due to heterogeneity rather than chance. We will take I2 values over 50% as suggestive of substantial heterogeneity but will take care to consider the direction and magnitude of effects.
Assessment of reporting biases
Where sufficient numbers of trials allow a meaningful presentation, funnel plots will be constructed to establish the potential influence of publication bias.
Data synthesis
If a sufficient number of comparable studies with low risk of bias are available we will carry out meta‐analyses in which studies will be weighted by size. While we will look for heterogeneity between studies (see above) we do not have any a priori expectation of this, hence we will use a fixed effects meta‐analysis. The meta‐analysis will be performed by CB and MF in the first instance.
Subgroup analysis and investigation of heterogeneity
As the objective of the review is to compare broadly similar treatments in broadly similar individuals we propose to carry out only one subgroup analysis comparing two equal groups representing studies with more training of practitioners and those with less.
Sensitivity analysis
We plan to carry out sensitivity analyses by limiting the analysis to studies with low or moderate risk of bias as determined by risk of bias domains, including:
1. Blinding of outcome assessors
2. Allocation concealment
3. Dropout rate lower than 20%
These sensitivity analyses will also be used to examine potential sources of methodological heterogeneity.
| Type of instrument | Name | references |
| Questionnaire | Abridged criteria | |
|
| PHQ‐15 | |
|
| SCL‐som | |
|
| Whiteley‐7 | |
| Interview | SCAN | |
|
| DIS | |
|
| CIDI | |
| Health care use | Frequent attendance | |
| The table may be supplemented by specific instruments for functional somatic syndromes The final review will also include a table of names and classification terms | ||
| Rubric | Reviewer 1 | Reviewer 2 | Conclusion | |
| Author name |
|
|
| |
| Title of paper |
|
|
| |
| Name of study |
|
|
| |
| Personal notes (e.g. name of disorder used) |
|
|
| |
| Reason for exclusion |
|
|
| |
| Study characteristics |
|
|
| |
|
| Assessment of methods (table 2) |
|
|
|
|
| Setting of the study (the primary care organisation) |
|
|
|
|
| Level of randomisation and measures of clustering |
|
|
|
|
| The risk of contamination (control patients receiving intervention unintentional or vice versa) |
|
|
|
|
| Doctor characteristics and sampling (previous training, years in practice, GP age) |
|
|
|
|
| Patient characteristics (inclusion, exclusion, ethnicity, diagnosis, symptom duration, psychiatric co‐morbidity) and sampling (population screening, waiting room screening, GP assessment, diagnostic instruments used) |
|
|
|
|
| Intervention* in active group |
|
|
|
|
| Intervention in control group |
|
|
|
|
| Outcome measure and instrument for assessment (primary outcome, secondary outcome, subgroups) |
|
|
|
|
| Length of maximum follow‐up |
|
|
|
|
| Results |
|
|
|
| * Interventions
| ||||
