Animal-assisted therapy for people with serious mental illness
This is the protocol for a review and there is no abstract. The objectives are as follows:
The objectives of this review are to identify the effectiveness of AAT as a treatment for patients with mental health illness. Studies excluded on methodological grounds may be used to describe the level of development of research in this field.
There have been many studies investigating the influence of pet ownership on human mental health and wellbeing, with some reporting positive effects (Cole 2007; Berget 2008; Villalta-Gil 2009). Studies have demonstrated reduced anxiety levels in college students studying for exams with pet interactions (Wilson 1991) and a reduced level of loneliness in cognitive care residences with animal-assisted therapy (AAT) (Barker 1998). A reduced level of loneliness in AIDS sufferers who are cat owners has also been demonstrated (Castelli 2001). In mental illness therapy, reduced fear level has been demonstrated in patients after a period of AAT prior to electroconvulsive therapy (Barker 2003).
Description of the condition
Serious mental illness involves persons of any age suffering from a mental illness that causes a psychotic episode (loss of personal subjective experience from the reality), which leads to hospitalisation for psychiatric care. Serious mental illnesses, such as schizophrenia, are conditions that disrupt a person's thinking, feeling, mood, ability to relate to others and daily functioning. Serious mental illnesses that will be the focus of this review include schizophrenia and other related disorders.
Description of the intervention
Animal-assisted therapy involves using any animal for the purpose of providing adjuvant therapy to patients. An animal trained in socialising with patients is used to assist in occupational therapy. The focus of this review will be dogs and cats though other animals are used for AAT. Horses and other farm animals have been used as a therapy for illnesses such as special needs assistance and autism, however, given the logistics associated with their use, they are generally not used in a hospitalised situation. Rabbits, fish and other small animals are also used as AAT but infrequently and provide different types of social interaction than dogs and cats. Given the differences and logistical issues associated with other animals, trials involving horses, rabbits, etc will be excluded from this review.
How the intervention might work
Exploring physical responses to stressful situations in a controlled environment, studies have demonstrated positive cardiovascular responses (lower blood pressure and heart rate; (Allen 2001) and autonomic responses (Allen 1991) when a pet was present during the test. Some researchers suggest that these results are as expected if pets were serving as a form of social support (Garrity 1989; Knight 2008). If humans have a good human social support structure, there have been reported health benefits. In particular, a good social support structure has been shown to protect against depression (Huang 2010) and suicide (Park 2010).
Why it is important to do this review
The use of AAT could be an effective method for increasing the wellbeing of psychiatric inpatients, reducing length of hospitalisation and reducing the need for medication. With the reduced length of stay and reduction in medication use, it will be a cost effective treatment with a low impact on environmental costs. There are some studies examining this area but these studies are often anecdotal or use small sample sizes. There is a certain level of uncertainty about the effects of AAT. A systematic review has yet to be carried out looking at AAT for mental illness. A systematic review on this subject would bring together the numerous studies in this area, to aid in making clinical decisions and guiding future research.
The objectives of this review are to identify the effectiveness of AAT as a treatment for patients with mental health illness. Studies excluded on methodological grounds may be used to describe the level of development of research in this field.
Criteria for considering studies for this review
Types of studies
All relevant randomised controlled trials. If a trial is described as 'double blind' but implies randomisation, we will include such trials in a sensitivity analysis ( see Sensitivity analysis). If their inclusion does not result in a substantive difference, they will remain in the analyses. If their inclusion does result in important clinically significant, but not necessarily statistically significant differences, we will not add the data from these lower quality studies to the results of the better trials, but will present such data within a subcategory. We will exclude quasi-randomised studies, such as those allocating by alternate days of the week. Where people are given additional treatments within AAT, we will only include data if the adjunct treatment is evenly distributed between groups and it is only the AAT that is randomised.
Types of participants
Any persons of any age after stabilisation from a psychotic episode. The participants may have a previously diagnosed mental illness or may be of unknown status on entering the study.
We are interested in making sure that information is as relevant to the current care of people with serious mental illness as possible so propose to clearly highlight the current clinical state (acute, early post-acute, partial remission, remission) as well as the stage (prodromal, first episode, early illness, persistent) and as to whether the studies primarily focused on people with particular problems (for example, negative symptoms, treatment-resistant illnesses).
Types of interventions
1. Any intervention designed as animal-assisted therapy (AAT)
AAT using dogs
AAT using cats
We will conduct a general analysis pooling both categories together, then proceed to analysing each category separately, and compare each category for primary outcomes.
2. Any other intervention or no intervention
Types of outcome measures
All outcomes will be divided into short term (less than six months), medium term (seven to 12 months) and long term (over one year).
1. Quality of life
For example, General Health Questionnaire, Warwick-Edinburgh Mental Wellbeing Scale, Patient Health Questionnaire - administered at the start, and at short-term, medium-term and long-term intervals by a qualified person i.e. doctor or occupational therapist.
1.1 Clinically important change in general quality of life or wellbeing scores.
1.2 Average change in general quality of life score or wellbeing scores.
2. Satisfaction with the intervention
2.1 Patients perception of benefit/harm of AAT.
3. Length of stay
3.1 Average length of stay in hospital/residential setting.
4. Mental state
For example, from Diagnostic and Statistical Manual of Mental Disorders
4.1 Clinically important change in general mental state score.
4.2 Average change in general mental state score.
4.3 Clinically important change in specific mental illness.
4.4 Average change in specific mental illness scores.
5. General functioning
5.1 Clinically important change in general functioning.
5.2 Average change in general functioning score.
6.1 Medication use at the start, and at short-term, medium-term and long-term intervals.
6.2 Avereage change in medication dosages.
7. Adverse Affects
8. 'Summary of findings' table
We will use the GRADE approach to interpret findings (Schünemann 2008) and will use GRADE profiler (GRADEPRO) to import data from RevMan 5 (Review Manager) to create 'Summary of findings' tables. These tables provide outcome-specific information concerning the overall quality of evidence from each included study in the comparison, the magnitude of effect of the interventions examined, and the sum of available data on all outcomes we will rate as important to patient care and decision making. We aim to select the following main outcomes for inclusion in the 'Summary of findings' table.
Quality of life
Satisfaction with the intervention
Length of stay
Search methods for identification of studies
We will search the Cochrane Schizophrenia Group MeerKat register using the phrase "*animal* or *dog * or *cat *" in title
This register is compiled by systematic searches of major databases, handsearches and conference proceedings (see group module).
Searching other resources
1. Reference searching
We will inspect references of all included studies for further relevant studies.
2. Personal contact
We will contact the first author of each included study for information regarding unpublished trials.
Data collection and analysis
Selection of studies
Review authors MD and RD will inspect citations from the searches and identify relevant abstracts. A random 20% sample will be independently re-inspected by review author FBH to ensure reliability. Where disputes arise, the full report will be acquired for more detailed scrutiny. Full reports of the abstracts meeting the review criteria will be obtained and inspected by MD and RD. FBH will re-inspect the reports in order to ensure reliable selection. Where it is not possible to resolve disagreement by discussion, we will attempt to contact the authors of the study for clarification.
Data extraction and management
To ensure reliability review authors MD and RD will independently extract data from all included studies. Again, any disagreement will be discussed, decisions documented and, if necessary, authors of studies will be contacted for clarification. With remaining problems FBH will help clarify issues and these final decisions will be documented. Data presented only in graphs and figures will be extracted whenever possible, but included only if two review authors independently have the same result. We will attempt to contact authors through an open-ended request in order to obtain missing information or for clarification whenever necessary. If studies are multi-centre, where possible, we will extract data relevant to each component centre separately.
We will extract data onto standard, simple forms.
2.2 Scale-derived data
We will include continuous data from rating scales only if:
a) the psychometric properties of the measuring instrument have been described in a peer-reviewed journal (Marshall 2000); and
b) the measuring instrument has not been written or modified by one of the trialists for that particular trial.
Ideally, the measuring instrument should either be i. a self-report or ii. completed by an independent rater or relative (not the therapist). We realise that this is not often reported clearly, in 'Description of studies' we will note if this is the case or not.
2.3 Endpoint versus change data
There are advantages of both endpoint and change data. Change data can remove a component of between-person variability from the analysis. On the other hand, calculation of change needs two assessments (baseline and endpoint) which can be difficult in unstable and difficult to measure in conditions such as schizophrenia. We have decided primarily to use endpoint data, and only use change data if the former are not available. Endpoint and change data will be combined in the analysis as we will use mean differences (MD) rather than standardised mean differences (SMD) throughout (Higgins 2011).
2.4 Skewed data
Continuous data on clinical and social outcomes are often not normally distributed. To avoid the pitfall of applying parametric tests to non-parametric data, we aim to apply the following standards to all data before inclusion:
a) standard deviations (SDs) and means are reported in the paper or obtainable from the authors;
b) when a scale starts from the finite number zero, the SD, when multiplied by two, is less than the mean (as otherwise the mean is unlikely to be an appropriate measure of the centre of the distribution, (Altman 1996);
c) if a scale started from a positive value (such as the Positive and Negative Syndrome Scale (PANSS), (Kay 1986)), which can have values from 30 to 210), the calculation described above will be modified to take the scale starting point into account. In these cases skew is present if 2 SD > (S-S min), where S is the mean score and 'S min' is the minimum score.
Endpoint scores on scales often have a finite start and end point and these rules can be applied. Skewed data pose less of a problem when looking at means if the sample size is large (> 200) and we will enter these data into the syntheses. We will present skewed endpoint data from studies of less than 200 participants as other data within the data and analysis section rather than enter such data into statistical analyses.
When continuous data are presented on a scale that includes a possibility of negative values (such as change data), it is difficult to tell whether data are skewed or not. We will present and enter change data into statistical analyses.
2.5 Common measure
To facilitate comparison between trials, we intend to convert variables that can be reported in different metrics, such as days in hospital (mean days per year, per week or per month) to a common metric (e.g. mean days per month).
2.6 Conversion of continuous to binary
Where possible, efforts will be made to convert outcome measures to dichotomous data. This can be done by identifying cut-off points on rating scales and dividing participants accordingly into 'clinically improved' or 'not clinically improved'. It is generally assumed that if there is a 50% reduction in a scale-derived score such as the Brief Psychiatric Rating Scale (BPRS, Overall 1962) or the PANSS (Kay 1986), this could be considered as a clinically significant response (Leucht 2005; Leucht 2005a). If data based on these thresholds are not available, we will use the primary cut-off presented by the original authors.
2.7 Direction of graphs
Where possible, we will enter data in such a way that the area to the left of the line of no effect indicates a favourable outcome for AAT. Where keeping to this makes it impossible to avoid outcome titles with clumsy double-negatives (e.g. 'Not improved') we will report data where the left of the line indicates an unfavourable outcome. This will be noted in the relevant graphs.
Assessment of risk of bias in included studies
Again, review authors MD and RD will work independently to assess risk of bias by using criteria described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) to assess trial quality. This set of criteria is based on evidence of associations between overestimate of effect and high risk of bias of the article such as sequence generation, allocation concealment, blinding, incomplete outcome data and selective reporting.
If the raters disagree, the final rating will be made by consensus, with the involvement of another member of the review group (FBH). Where inadequate details of randomisation and other characteristics of trials are provided, we will contact authors of the studies in order to obtain further information. Non-concurrence in quality assessment will be reported, but if disputes arise as to which category a trial is to be allocated, again, we will resolve these by discussion.
The level of risk of bias will be noted in both the text of the review and in the 'Summary of findings' table.
Measures of treatment effect
1. Binary data
For binary outcomes, we will calculate a standard estimation of the risk ratio (RR) and its 95% confidence interval (CI). It has been shown that RR is more intuitive (Boissel 1999) than odds ratios and that odds ratios tend to be interpreted as RR by clinicians (Deeks 2000). The Number Needed to Treat/Harm (NNT/H) statistic with its CIs is intuitively attractive to clinicians but is problematic both in its accurate calculation in meta-analyses and interpretation (Hutton 2009). For binary data presented in the 'Summary of findings' table/s, where possible, we will calculate illustrative comparative risks.
2. Continuous data
For continuous outcomes, we will estimate mean difference (MD) between groups. We prefer not to calculate effect size measures (standardised mean difference SMD). However, if scales of very considerable similarity are used, we will presume there is a small difference in measurement, and we will calculate effect size and transform the effect back to the units of one or more of the specific instruments.
Unit of analysis issues
1. Cluster trials
Studies increasingly employ 'cluster randomisation' (such as randomisation by clinician or practice) but analysis and pooling of clustered data poses problems. Firstly, authors often fail to account for intra-class correlation in clustered studies, leading to a 'unit of analysis' error (Divine 1992) whereby P values are spuriously low, CIs unduly narrow and statistical significance overestimated. This causes type I errors (Bland 1997; Gulliford 1999).
Where clustering is not accounted for in primary studies, we will present data in a table, with a (*) symbol to indicate the presence of a probable unit of analysis error. In subsequent versions of this review we will seek to contact first authors of studies to obtain intra-class correlation coefficients (ICCs) for their clustered data and to adjust for this by using accepted methods (Gulliford 1999). Where clustering has been incorporated into the analysis of primary studies, we will present these data as if from a non-cluster randomised study, but adjust for the clustering effect.
We have sought statistical advice and have been advised that the binary data as presented in a report should be divided by a 'design effect'. This is calculated using the mean number of participants per cluster (m) and the ICC [Design effect = 1+(m-1)*ICC] (Donner 2002). If the ICC is not reported, it will be assumed to be 0.1 (Ukoumunne 1999).
If cluster studies have been appropriately analysed taking into account ICCs and relevant data documented in the report, synthesis with other studies will be possible using the generic inverse variance technique.
2. Cross-over trials
A major concern of cross-over trials is the carry-over effect. It occurs if an effect (e.g. pharmacological, physiological or psychological) of the treatment in the first phase is carried over to the second phase. As a consequence, on entry to the second phase the participants can differ systematically from their initial state despite a wash-out phase. For the same reason, cross-over trials are not appropriate if the condition of interest is unstable (Elbourne 2002). As both effects are very likely in severe mental illness, we will only use data of the first phase of cross-over studies.
3. Studies with multiple treatment groups
Where a study involves more than two treatment arms, if relevant, the additional treatment arms will be presented in comparisons. If data are binary, these will be simply added and combined within the two-by-two table. If data are continuous, we will combine data following the formula in section 18.104.22.168 (Combining groups) of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). Where the additional treatment arms are not relevant, we will not use these data.
Dealing with missing data
1. Overall loss of credibility
At some degree of loss of follow-up, data must lose credibility (Xia 2009). We choose that, for any particular outcome, should more than 50% of data be unaccounted for, we will not reproduce these data or use them within analyses. If, however, more than 50% of those in one arm of a study are lost, but the total loss is less than 50%, we will address this within the 'Summary of findings' table/s by down-rating quality. Finally, we will also downgrade quality within the 'Summary of findings' table/s should loss be 25% to 50% in total.
In the case where attrition for a binary outcome is between 0% and 50% and where these data are not clearly described, we will present data on a 'once-randomised-always-analyse' basis (an intention-to-treat (ITT) analysis). Those leaving the study early are all assumed to have the same rates of negative outcome as those who completed, with the exception of the outcome of death and adverse effects. For these outcomes, the rate of those who stay in the study - in that particular arm of the trial - will be used for those who did not. We will undertake a sensitivity analysis to test how prone the primary outcomes are to change when data only from people who complete the study to that point are compared to the ITT analysis using the above assumptions.
In the case where attrition for a continuous outcome is between 0% and 50%, and data only from people who complete the study to that point are reported, we will reproduce these.
3.2 Standard deviations
If standard deviations (SDs) are not reported, we will first try to obtain the missing values from the authors. If not available, where there are missing measures of variance for continuous data, but an exact standard error (SE) and confidence intervals (CIs) available for group means, and either the 'P' value or 't' value are available for differences in mean, we can calculate them according to the rules described in the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011): When only the SE is reported, SDs are calculated by the formula SD = SE * square root (n). Chapters 7.7.3 and 16.1.3 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011) present detailed formulae for estimating SDs from P values, t or F values, CIs, ranges or other statistics. If these formulae do not apply, we will calculate the SDs according to a validated imputation method which is based on the SDs of the other included studies (Furukawa 2006). Although some of these imputation strategies can introduce error, the alternative would be to exclude a given study’s outcome and thus to lose information. We nevertheless will examine the validity of the imputations in a sensitivity analysis excluding imputed values.
3.3 Last observation carried forward
We anticipate that in some studies the method of last observation carried forward (LOCF) will be employed within the study report. As with all methods of imputation to deal with missing data, LOCF introduces uncertainty about the reliability of the results (Leucht 2007). Therefore, where LOCF data have been used in the trial, if less than 50% of the data have been assumed, we will present and use these data and indicate that they are the product of LOCF assumptions.
Assessment of heterogeneity
1. Clinical heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge clinical heterogeneity. We will simply inspect all studies for clearly outlying people or situations which we had not predicted would arise. When such situations or participant groups arise, these will be fully discussed.
2. Methodological heterogeneity
We will consider all included studies initially, without seeing comparison data, to judge methodological heterogeneity. We will simply inspect all studies for clearly outlying methods which we had not predicted would arise. When such methodological outliers arise these will be fully discussed.
3. Statistical heterogeneity
3.1 Visual inspection
We will visually inspect graphs to investigate the possibility of statistical heterogeneity.
3.2 Employing the I2 statistic
Heterogeneity between studies will be investigated by considering the I2 method alongside the Chi2 'P' value. The I2 provides an estimate of the percentage of inconsistency thought to be due to chance (Higgins 2003). The importance of the observed value of I2 depends on i. magnitude and direction of effects and ii. strength of evidence for heterogeneity (e.g. 'P' value from Chi2 test, or a CI for I2). An I2 estimate greater than or equal to around 50% accompanied by a statistically significant Chi2 statistic, will be interpreted as evidence of substantial levels of heterogeneity (Section 9.5.2 - Higgins 2011). When substantial levels of heterogeneity are found in the primary outcome, we will explore reasons for heterogeneity (Subgroup analysis and investigation of heterogeneity).
Assessment of reporting biases
1. Protocol versus full study
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. These are described in section 10.1 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). We will try to locate protocols of included randomised trials. If the protocol is available, outcomes in the protocol and in the published report will be compared. If the protocol is not available, outcomes listed in the methods section of the trial report will be compared with actually reported results.
2. Funnel plot
Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results (Egger 1997). These are again described in Section 10 of the Cochrane Handbook for Systemic reviews of Interventions (Higgins 2011). We are aware that funnel plots may be useful in investigating reporting biases but are of limited power to detect small-study effects. We will not use funnel plots for outcomes where there are 10 or fewer studies, or where all studies are of similar sizes. In other cases, where funnel plots are possible, we will seek statistical advice in their interpretation.
We understand that there is no closed argument for preference for use of fixed-effect or random-effects models. The random-effects method incorporates an assumption that the different studies are estimating different, yet related, intervention effects. This often seems to be true to us and the random-effects model takes into account differences between studies, even if there is no statistically significant heterogeneity. There is, however, a disadvantage to the random-effects model. It puts added weight onto small studies, which often are the most biased ones. Depending on the direction of effect, these studies can either inflate or deflate the effect size. We choose the fixed-effect model for all analyses. The reader is, however, able to choose to inspect the data using the random-effects model.
Subgroup analysis and investigation of heterogeneity
1. Subgroup analyses
We have chosen to include all ages and anticipate subgroup analysis of "adults" and "children < 18 years of age".
1.2 Physical illness and no physical illness
We have chosen to include mentally ill people with or without co-morbid physical illness and we anticipate subgroup analyses investigating "physical illness" and "no physical illness".
1.3 Clinical state, stage or problem
We propose to undertake this review and provide an overview of the effects of AAT for people with severe mental illness. In addition, however, we will try to report data on subgroups of people in the same clinical state, stage and with similar problems.
1.4 Residential psychiatric facilities
We have chosen to include all mentally ill patients and anticipate subgroup analysis of those who are undergoing treatment in residential care.
2. Investigation of heterogeneity
If inconsistency is high, this will be reported. First, we will investigate whether data have been entered correctly. Second, if data are correct, we will visually inspect the graph and outlying studies will be successively removed to see if homogeneity is restored. For this review, we have decided that should this occur with data contributing to the summary finding of no more than around 10% of the total weighting, data will be presented. If not, data will not be pooled and issues will be discussed. We know of no supporting research for this 10% cut-off but are investigating use of prediction intervals as an alternative to this unsatisfactory state.
When unanticipated clinical or methodological heterogeneity are obvious, we will simply state hypotheses regarding these for future reviews or versions of this review. We do not anticipate undertaking analyses relating to these.
1. Implication of randomisation
We aim to include trials in a sensitivity analysis if they are described in some way as to imply randomisation. For the primary outcomes, we will include these studies and if there is no substantive difference when the implied randomised studies are added to those with better description of randomisation, then all data will be employed from these studies.
2. Assumptions for lost binary data
Where assumptions have to be made regarding people lost to follow-up (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. If there is a substantial difference, we will report results and discuss them, but will continue to employ our assumption.
Where assumptions have to be made regarding missing SDs data (see Dealing with missing data), we will compare the findings of the primary outcomes when we use our assumption/s and when we use data only from people who complete the study to that point. A sensitivity analysis will be undertaken to test how prone results are to change when completer-only data only are compared to the imputed data using the above assumption. If there is a substantial difference, we will report results and discuss them, but will continue to employ our assumption.
3. Risk of bias
We will analyse the effects of excluding trials that are judged to be at high risk of bias across one or more of the domains of randomisation (implied as randomised with no further details available) allocation concealment, blinding and outcome reporting for the meta-analysis of the primary outcome. If the exclusion of trials at high risk of bias does not substantially alter the direction of effect or the precision of the effect estimates, then data from these trials will be included in the analysis.
4. Imputed values
We will also undertake a sensitivity analysis to assess the effects of including data from trials where we used imputed values for ICC in calculating the design effect in cluster randomised trials.
If substantial differences are noted in the direction or precision of effect estimates in any of the sensitivity analyses listed above, we will not pool data from the excluded trials with the other trials contributing to the outcome, but will present them separately.
5. Fixed and random effects
All data will be synthesised using a fixed-effect model, however, we will also synthesise data for the primary outcome using a random-effects model to evaluate whether this alters the significance of the results.
The Centre for Evidence-based Veterinary Medicine is supported by an unrestrictive grant from Novartis Animal Health and The University of Nottingham.
The Cochrane Schizophrenia Group Editorial Base in Nottingham produces and maintains standard text for use in the Methods section of their reviews. We have used this text as the basis of what appears here and adapted it as
We would like to thank Zunaira Javed for peer reviewing this protocol.
Contributions of authors
Martin Downes - proposed the review, helped write the protocol, will contribute to formulating searches, study selection, data extraction, and writing the review.
Rachel Dean - helped write the protocol, will contribute to formulating searches, study selection and writing the review.
Fiona Bath-Hextall - helped write the protocol, will contribute to study selection and writing the review.
Declarations of interest
The authors are aware of no known conflicts of interest.
Sources of support
Novartis Animal Health, UK.
The Centre for Evidence-based Veterinary Medicine is supported by an unrestricted grant from Novartis Animal Health