PEER REVIEW HISTORY ARTICLE DETAILS TITLE (PROVISIONAL)

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1 PEER REVIEW HISTORY BMJ Open publishes all reviews undertaken for accepted manuscripts. Reviewers are asked to complete a checklist review form ( and are provided with free text boxes to elaborate on their assessment. These free text comments are reproduced below. TITLE (PROVISIONAL) AUTHORS REVIEWER REVIEW RETURNED GENERAL COMMENTS ARTICLE DETAILS Inequalities in physical co-morbidity: A longitudinal comparative cohort study of people with severe mental illness in the UK Reilly, Siobhan; Olier, Ivan; Planner, Claire; Doran, Tim; Reeves, David; Ashcroft, Darren; Gask, Linda; Kontopantelis, Evangelos VERSION 1 - REVIEW Susan Smith RCSI, Dublin, Ireland 10-Jul-2015 Thank you for asking me to review this paper on inequalities in physical co-morbidities in people with severe mental illness (SMI). It is an interesting paper and original in that it reports longitudinal data to allow comparison over time and a lot of work has gone into this paper. However, it is quite limited in that it is a simple descriptive analysis over time and does not incorporate any analysis of potential confounders (all acknowledged by the authors). I have the following comments: The authors present simple descriptive statistics in various time frames and they justify doing this in the discussion but I did wonder about potential confounding in an observational study such as this and this is not really addressed or discussed. Why could you not collect data within CPRD on BMI and smoking status and other potential confounders that could have been included in a more analytic model. Alternatively, could the matching not have included some of these likely significant confounders. Perhaps include reason why this was not done as his data would be available in GP records The descriptive patterns that emerge are not that surprising given the existing knowledge about the effects of newer anti-psychotic drugs on metabolism and the link between deprivation and mental health problems Limitations of CPRD? while the is a large dataset does it have representative cover my understanding is that more deprived practices are under-represented which would influence this study Abstract: o Study design described as cohort but seems more like casecontrol due to sampling of matched cases rather than taking dull database o SMI definition would be good in abstract o inequalities rose for most conditions not sure what this means o why just comment on variation within SMI group should this not be compared to variation in full group or in controls Abstract and overall study conclusions: Many papers presenting epidemiological data on multimorbidity conclude with fact that need targeted interventions for this group which is no longer a novel idea. For the abstract, it would be good if conclusions could be more

2 REVIEWER REVIEW RETURNED GENERAL COMMENTS specific and relate to the actual findings of this study and what they tell us about who to target etc The full conclusions are a bit more specific but the discussion generally could be stronger on practice and policy implications of the findings and what we know of current management of physical co-morbidities in SMI and where this work fits in etc Intro: statement on line 45 that GPs may be reluctant to participate in care is justified using quite old references. Is here anything more recent especially around exception reporting within QoF as this would be where you would expect to see evidence of people with SMI being opted out of care Analysis: Would be good to have more information on mapping approach and a reference for it, if appropriate perhaps is just a descriptive technique. There is now quite a lot of literature on analysis of clustering of conditions in multimorbidity (see which may be worth mentioning in the discussion and also may be mnore suited to full cohort datasets Discussion: the authors refer to the previous national studies of multimorbidity by Barnett et al in Scotland and Salisbury et al in England but they don t actually compare them which they could do for the related time frame No discussion about results relating to medication prescribing changes over time and variation Minor issues: No ref for Smith et al on page 7, line 42 Table 1: Mean number conditions. I presume this is mean number of additional conditions (i.e as well as SMI) as controls automatically have one less condition (SMI) Multimorbidity is not usually hyphenated and this varies throughout the text Joseph Hayes Division of Psychiatry, UCL United Kingdom 16-Jul-2015 This is a large electronic health records study of prevalence of severe mental illness (SMI) by year from , distribution of SMI by geographical region, distribution of SMI by area level deprivation, prevalence of specific SMI diagnosis by year, prevalence of antipsychotic prescribing by year, prevalence of antidepressant describing by year, prevalence of 16 common physical health conditions by specific SMI diagnosis, and prevalence of 2 of these common physical health conditions (i.e 16x16 further comparisons). The paper as it stands is difficult to read. In the most part this is by virtue of trying to cover too much and because of the number of topics investigated, each is tackled in a superficial manner. Also, despite having a matched control group the authors make no direct comparisons (i.e relative risk) with this frequency matched comparison group. Finding the relevant data that a clinician or researcher may be interested in will be a challenge. I think this is then reflected in the rather vague abstract and discussion section. It may be beneficial to break the manuscript into a number of shorter papers that can be more focused. The information contained within

3 could be a useful addition to the literature on SMI prevalence and comorbidity in the UK if presented more clearly. Below I clarify my responses to the specific questions asked in the Review Checklist: Is the research question or study objective clearly defined? The study describes two aims (page 4, line 1-9) but, as I have described above, far more is included in the manuscript. Is the abstract accurate, balanced and complete? Given the amount of data in the manuscript, very little is communicated in the abstract. It is also quite vague and the conclusion is weak. If statistics are used are they appropriate and described fully? The paper is limited to presenting % prevalence. Do the results address the research question or objective? Again, the results are more comprehensive than the research objectives. Are they presented clearly? The prose of the results section is difficult to follow because of the number of results being reported. There are a large number of tables, appendix tables and figures. The figures (Figure 2 and Figure A2) are very difficult to comprehend and appear to reproduce data in tables A3 and A4 respectively. These figures do not add to the manuscript or improve communication of the findings. Are the discussion and conclusions justified by the results? (Page 6, line 53-54) I disagree that this is the first study to explore prevalence of SMI and comorbidity in the context of deprivation. For example Smith et al. (2013). Schizophrenia is associated with excess multiple physical-health comorbidities but low levels of recorded cardiovascular disease in primary care: cross-sectional study. BMJ open, 3(4), e and Osborn et al. (2007). Relative risk of cardiovascular and cancer mortality in people with severe mental illness from the United Kingdom's General Practice Research Database. Archives of general psychiatry, 64(2), have addressed elements of this issue. (Page 7, line 1-3) The age of the cohort with SMI reduced over time by I m not sure you can say the age at which people received their diagnosis lowered over the 12 years as these are not incident cases. Are you suggesting the mean age of SMI onset is >50? (Page 7, line 14-15) Would you expect your results to be the same as QOF SMI prevalence? Essentially GPs can decide what constitutes SMI to be added to their SMI register, so will tend to include patients beyond those with schizophrenia, bipolar disorder and other non-organic psychoses. QOF existed from 2004 (and no longer exists) so this may be the reason for the apparent increase in prevalence. Also, you have not shown that this increase is significant. (Page 7, line 8-9) Sentences like A variable pattern of comorbidity was observed across different SMI subgroups and areas of high and low depravation do little to inform the reader what the results of this study are.

4 (Page 7, line 26) You suggest that increases in prevalence may be linked to increases in illicit drug use, but the reference does not show that there has been an increase in illicit drug use. (Page 7, line 53) Because of your reporting of the data I am not sure there is an upward trend in comorbidity. (Page 8, line 6-9) This sentence doesn t quite make sense. Do you mean that the cost of co-morbidity is greater than additive? (Page 8, line 25) Your results are purely descriptive, so I m not sure that unmeasured confounding is an issue. (Page 8, line 25-26) Here you say you matched for depravation (at the practice level) but in the abstract you say you matched for practice. Which did you do? (Page 8, line 28) I m unclear why you think obesity and smoking status may not be recorded accurately. Even ethnicity is pretty well recorded in CPRD. (Page 8, line 29-35) I think you are right not to perform a multitude of hypothesis tests, but this comes back to my earlier points about vague and multiple objectives and too much data to communicate. Some reporting of risk relative to the comparison group would not be inappropriate as otherwise what is the benefit of including this group? I agree that large data sets will give small P-values but this is not a reason to avoid any comparison. Also you are free to define your own significance level so this is not a major problem I you did which to test hypotheses. (Page 8, line 35-37) I think this sentence needs restructuring. Do you mean that LSOA IMD of the GP practice is not a good proxy for individual level depravation? Is this important, given that you are talking about the services the practice may provide? This is only a limitation if you were trying to use area IMD as a measure of individual level depravation. (Page 8, line 40-45) I worry that in this section you are proposing that any research into SMI using EHR is invalid because of difficulties around diagnosis. There is evidence that SMI recording is valid in primary care records, for example: Nazareth et al. (1993). Accuracy of diagnosis of psychosis on general practice computer system. Bmj, 307(6895), There is also evidence of diagnostic stability over time: Hardoon et al.(2013). Recording of severe mental illness in United Kingdom primary care, (Page 8, line 51) I am unsure if these data show rising inequalities in the pattern and number of different comorbidities as this has not been tested. (Page 8-9, line 55-4) I m unsure how the comorbidity results could be helpful in planning trials? Further Comments Abstract (Page 2, line 40) inequalities rose for most conditions this is not clear, do you mean practices in the most deprived areas saw the

5 Reviewer #1 biggest increase in comorbid conditions? The results section of the abstract should probably report more numerical results (given that you have so many). Introduction (Page 3, line 33-41) This sentence is very long, and as a result is difficult to comprehend. (Page 3, line 51-52) There are longitudinal studies of comorbidity in SMI, and it is probably appropriate to refer to some of these. (Page 4, 1-4) Aim 1 could benefit from a full stop or being broken up into the multiple aims described. Methods (Page 4, Line 28-30) Is the consistent with the inclusion criteria for SMI registers group described here the Other SMI group in the tables? This should be clarified who are these people? (Page 4, line 54-55) As mentioned above the Methods section and Discussion sections have different definitions of frequency matching. (Page 5, line 2-3) IMD was elicited from the practice postcode. I m unclear how you did this as a different measure of IMD is used in Scotland which does not map onto IMDs for England. It would be helpful to the reader if this was described more fully, including an overview of what IMD captures. Results (Page 6, line 21-24) The sentence Notable exceptions were coronary heart disease and heart failure; rates fell for both groups, as well as stroke, rates remained relatively stable for the SMI group but fell for controls does not read well. VERSION 1 AUTHOR RESPONSE 1. The authors present simple descriptive statistics in various time frames and they justify doing this in the discussion but I did wonder about potential confounding in an observational study such as this and this is not really addressed or discussed. Why could you not collect data within CPRD on BMI and smoking status and other potential confounders that could have been included in a more analytic model. Alternatively, could the matching not have included some of these likely significant confounders. Perhaps include reason why this was not done as his data would be available in GP records That is a good point which we ourselves raise and discuss in the strengths and limitations section. We did not collect data on BMI and smoking status and other potential confounders for three reasons. First, assuming such a strict matching process is desirable, information on the variables we would like to control are often missing in the CPRD (BMI would be missing for between 5-80% of patients depending on year and condition, ethnicity and alcohol abuse are under-reported and smoking, although the most reliable of all, still has some reliability issues). Second, matching on these variables would have substantially reduced our sample. Third and most importantly, we are not convinced a strict matching is desirable since there would be a risk of controlling for the differences we wish to quantify. That is, in the first instance we are interested in quantifying the differences in physical comorbidities between groups, even if they may be attributable to external factors and the exact path

6 of the disease progression is unclear. We have expanded the respective section slightly (considering the size of the paper) to make this clearer: rather quantify overall differences in physical comorbidity irrespective of the potential underlying factors (hence through a much stricter matching would be at risk of over-controlling) [strengths and limitations section in the discussion] 2. The descriptive patterns that emerge are not that surprising given the existing knowledge about the effects of newer anti-psychotic drugs on metabolism and the link between deprivation and mental health problems We agree that many of the results are in the direction expected. However, no other studies have presented this this data on SMI prevalence rates by country, region and deprivation quintiles over a 12 year period, or for 16 chronic conditions or highlighted the differences between those registered in practices in more affluent and more deprived areas. Having clear results with descriptive patterns presented in this way provides commissioners with further evidence to ensure that primary and secondary care have a clear and coordinated remit for monitoring physical health and intervening to prevent the onset of diseases that contribute to the significantly higher mortality rate experienced by this group of patients. 3. Limitations of CPRD? while the is a large dataset does it have representative cover my understanding is that more deprived practices are under-represented which would influence this study The main limitation of the CPRD is the fact that it recruits practices with a single computer system, VISION (although now they are starting to recruit EMIS practices as well), and that there have been differences across systems. They are actually pretty balanced on deprivation compared to the UK and England, the only difference to all English practices is that CPRD practices tend to be larger than average. We had added a reference from previous work were a detailed comparison between the CPRD and England was presented but now we have now added this to the discussion to make this clearer: Although the CPRD is representative of the UK in its distribution of practice location deprivation it tends to recruit larger than average practices, while the version we analysed only included practices utilising one of the numerous clinical computer systems available (VISION). Although differences in performance across systems have been observed, such issues may be less relevant in this setting where we focus on prevalence rates. 4. Abstract: Study design described as cohort but seems more like case-control due to sampling of matched cases rather than taking dull database A cohort study does not necessarily imply the comparator cohort being the full database. A casecontrol study is defined by the outcome in question, when one is investigated of course. For example, if the outcome in question was diabetes in 2012 we would match diabetes and non-diabetes cases on age and sex and retrospectively quantify SMI rates for the two groups. 5. Abstract: SMI definition would be good in abstract : Given the limited word count of the abstract we have included our definition in the method section SMI was defined as: schizophrenia, affective disorder (divided into bipolar or unspecified affective disorder) or other types of psychoses, consistent with the inclusion criteria for SMI registers in primary care general practice in the UK as part of the Quality and Outcomes Framework (QOF) financial incentive scheme. The QOF was introduced in 2004 and links general practitioner s (GP) pay with achievement of targets set across a range of chronic conditions.

7 6. Abstract: inequalities rose for most conditions not sure what this means : Thank you for spotting this. We have revised this to The gap between the prevalence of those with and without SMI increased over time for most conditions. [results section, 2 nd paragraph] 7. Abstract: why just comment on variation within SMI group should this not be compared to variation in full group or in controls : Thank you for highlighting this we have now revised this sentence in the abstract: Most conditions were more prevalent the most deprived areas for both groups, whereas other conditions such as hypothyroidism, chronic kidney disease and cancer were more prevalent in more affluent areas and these differences were greater for the SMI group. 8. Abstract and overall study conclusions: Many papers presenting epidemiological data on multimorbidity conclude with fact that need targeted interventions for this group which is no longer a novel idea. For the abstract, it would be good if conclusions could be more specific and relate to the actual findings of this study and what they tell us about who to target etc The full conclusions are a bit more specific but the discussion generally could be stronger on practice and policy implications of the findings and what we know of current management of physical co-morbidities in SMI and where this work fits in etc : Thank you for your suggestions. The conclusions in the abstract have been amended and the discussion and final conclusions are now stronger, more specific and relate to implications for current policy and practice. 9. Intro: statement on line 45 that GPs may be reluctant to participate in care is justified using quite old references. Is here anything more recent especially around exception reporting within QoF as this would be where you would expect to see evidence of people with SMI being opted out of care : This is a good point. We have added a more recent reference (Roberts and Bailey, 2011) and widened the point to system and individual actions that are necessary to address gaps in the treatment of physical health in people with SMI. In work that is under review with BMJ Qual Saf we have investigated patient level predictors of exception reporting within the QOF context, by type (due to contraindication, informed dissent or other / generic exception), and here an excerpt from one of the results tables: Odds Ratios (99% Confidence interval) Conditions # All reasons* Clinical contraindication Informed dissent Atrial fibrillation 3.11(3.00,3.22) 5.33(5.11,5.56) 1.06(1.02,1.11) Asthma 4.97(4.86,5.09) 2.85(2.77,2.93) 4.58(4.47,4.69) Hypertension 1.47(1.44,1.50) 1.71(1.67,1.76) 1.15(1.13,1.18) Cancer 0.96(0.93,0.99) 1.18(1.14,1.22) 0.80(0.78,0.83) Coronary heart disease 9.82(9.54,10.11) 23.71(22.87,24.58) 2.20(2.14,2.27) Heart failure 1.83(1.74,1.92) 2.54(2.40,2.70) 0.98(0.93,1.03) Chronic kidney disease 1.82(1.78,1.87) 2.43(2.36,2.51) 1.08(1.05,1.11) COPD 5.84(5.63,6.07) 9.20(8.78,9.64) 2.24(2.15,2.33) Dementia 2.24(2.13,2.37) 3.25(3.04,3.46) 1.02(0.96,1.09)

8 Odds Ratios (99% Confidence interval) Clinical All reasons* contraindication Informed dissent Depression 0.94(0.92,0.96) 1.81(1.76,1.85) 0.52(0.51,0.53) Diabetes mellitus 6.35(6.20,6.51) 5.06(4.91,5.22) 5.38(5.25,5.52) Epilepsy 5.30(5.01,5.60) 11.76(11.00,12.59) 1.37(1.29,1.47) Learning disability 1.10(1.00,1.22) 1.75(1.54,1.99) 0.66(0.58,0.75) Severe mental illness 4.38(4.17,4.60) 4.42(4.15,4.70) 2.83(2.68,2.98) Stroke 3.61(3.48,3.73) 3.84(3.68,4.01) 2.44(2.35,2.53) Hypothyroidism 0.87(0.84,0.90) 0.93(0.89,0.96) 0.84(0.81,0.87) * Clinical contraindication, informed dissent or reason unknown. # Reference: patients without the specific condition, but with one or more other study conditions. As we can see on the table which reports the odds of being excepted from QOF care standards, exception rates for SMI at the patient level (i.e. after controlling for comorbidities and other characteristics) are on the higher end but not the highest. We have also tried to mention this work, although this poses challenges since it is still under review: which is reflected in the likelihood of patients being opted out (appropriately or not) but also refusing treatment. [introduction, 1 st paragraph] 10. Analysis: Would be good to have more information on mapping approach and a reference for it, if appropriate perhaps is just a descriptive technique. There is now quite a lot of literature on analysis of clustering of conditions in multimorbidity (see which may be worth mentioning in the discussion and also may be more suited to full cohort datasets : Thank you for this. Indeed quantifying comorbidity can be methodologically complex with various indices available. In this context of comorbidity mapping as the presence of two conditions, there is little in terms of methodological innovation that can be referenced. However, thank you for pointing out this relevant piece of work to us, which we now reference in the method section:, a common practice when investigating disease clusters, We have also added a section in discussion on this issue, referenced this study and drawn comparison with other relevant data, though few have published results on multiple comorbidities. 11. Discussion: the authors refer to the previous national studies of multimorbidity by Barnett et al in Scotland and Salisbury et al in England but they don t actually compare them which they could do for the related time frame : Both of these studies do not focus on SMI and we have made this clearer where they are both referenced in this paper. In the discussion we had made some comparisons to the relevant literature but we have now expanded this section, where possible, discussing the relevant timeframes and made it clearer where this was not possible too. 12. No discussion about results relating to medication prescribing changes over time and variation : We outline medication prescribing over the period in the results section: The number of individuals with one or more prescription for 1st generation antipsychotic medications has steadily declined over the 12 years (from 20.26% to 9.78%), whereas 2nd generation anti-psychotic medications have steadily increased (from 18.1% to 43%). Decreases in depot injections were observed over time as shown in Table 3. An increase over the time period was observed for selective serotonin re-uptake

9 inhibitors (SSRI) (from 18.1% to 25.75%) whereas a decrease was observed for both tricyclic antidepressants (from 14.03% to 9.21%). We have added the following to the 3 rd paragraph in the discussion. It is possible that the increased number of conditions is linked with increased prescriptions of 2 nd generation anti-psychotic medications along with relevant references. Minor issues: 13. No ref for Smith et al on page 7, line 42 : Thank you for pointing this out, this has now been added. 14. Table 1: Mean number conditions. I presume this is mean number of additional conditions (i.e as well as SMI) as controls automatically have one less condition (SMI) : This has been clarified in table 1 and text. 15. Multimorbidity is not usually hyphenated and this varies throughout the text : This has been corrected. Reviewer: #2 1. The paper as it stands is difficult to read. In the most part this is by virtue of trying to cover too much and because of the number of topics investigated, each is tackled in a superficial manner. Also, despite having a matched control group the authors make no direct comparisons (i.e relative risk) with this frequency matched comparison group. Finding the relevant data that a clinician or researcher may be interested in will be a challenge. I think this is then reflected in the rather vague abstract and discussion section. It may be beneficial to break the manuscript into a number of shorter papers that can be more focused. The information contained within could be a useful addition to the literature on SMI prevalence and comorbidity in the UK if presented more clearly. We feel our revised paper addresses your helpful suggestions with improvements to the writing in the abstract and discussion. Further text has been added and a table has been moved to the appendices. Further edits to the abstract would take us over the 300 word limit, but we have made some edits to it to incorporate more results (see also response to comment #3 below) with specific conclusions addressing policy and practice implications. The discussion has been extended and edited so that the results are discussed with more clarity. We appreciate your steer to split this paper into two papers, however, it might help if we explain our rationale for presenting these results in one paper. As authors of a relatively low-cost study where the research team is no longer funded on this work, we are keen to have the results in the public domain at the earliest opportunity so that they can be the discussion of future guidance and policy (which we have now highlighted in the conclusion). In addition, given the policy steer in this area for the NHS (e.g. see Medical Directorate NHS England. Our Ambition to Reduce Premature Mortality: A resource to support commissioners in setting a level of ambition. NHS England, 2014) we feel that commissioners and policy makers would appreciate these results sooner rather than later. As we note in the discussion Having up to date epidemiological data helps to pinpoint how healthcare providers need to meet the challenge of providing good quality treatment and care to people with SMI. We have revised the manuscript and added further description, clarification and discussion.

10 2. Is the research question or study objective clearly defined? The study describes two aims (page 4, line 1-9) but, as I have described above, far more is included in the manuscript. Thank you - we have revised the aims so they better reflect what we have covered in this manuscript. 3. Is the abstract accurate, balanced and complete? Given the amount of data in the manuscript, very little is communicated in the abstract. It is also quite vague and the conclusion is weak. We acknowledge this issue which largely stems from the 300 word abstract limit, to which we must adhere. It is impossible to discuss all aspects of the paper in the abstract, nevertheless, we have now edited the conclusion and provided further data in the abstract. 4. The prose of the results section is difficult to follow because of the number of results being reported. There are a large number of tables, appendix tables and figures. The figures (Figure 2 and Figure A2) are very difficult to comprehend and appear to reproduce data in tables A3 and A4 respectively. These figures do not add to the manuscript or improve communication of the findings. Thank you for highlighting that the results section needed improving. This has now been addressed with further text added. Regarding the graphs and tables we appreciate they provide the same information but they do so in different ways. Although the tables are more useful when detail is needed, the graphs can provide an easy to digest overview which is essential in this complex piece of work. We have added in each of the graph/ table headings what other table/ graph they are linked to. The graphs are similar to those published by Guthrie and colleagues (2012) and highlight the patterns of comorbidities that are most common so they are an important aspect of this paper and aspects that can be compared directly in future reviews in this area. We would prefer to keep both tables and graphs in, but perhaps the editor could provide guidance on this. 5. Are the discussion and conclusions justified by the results? (Page 6, line 53-54) I disagree that this is the first study to explore prevalence of SMI and comorbidity in the context of deprivation. For example Smith et al. (2013). Schizophrenia is associated with excess multiple physical-health comorbidities but low levels of recorded cardiovascular disease in primary care: cross-sectional study. BMJ open, 3(4), e and Osborn et al. (2007). Relative risk of cardiovascular and cancer mortality in people with severe mental illness from the United Kingdom's General Practice Research Database. Archives of general psychiatry, 64(2), have addressed elements of this issue. Both of these studies were originally cited and discussed and we have now clarified better how we think our study is a first. This study is not the first to explore prevalence and comorbidity in the context of deprivation but to our knowledge, it is the first to do this over a 12 year period for a SMI population and for a large number of comorbidities. The conclusions have also been improved as suggested by the first reviewer. 6. (Page 7, line 1-3) The age of the cohort with SMI reduced over time by I m not sure you can say the age at which people received their diagnosis lowered over the 12 years as these are not incident cases. Are you suggesting the mean age of SMI onset is >50? This statement relates to the findings that were stated on page 5. The mean number of years since the first SMI diagnosis increased from 11.7 (sd 11.5) in 2000/1 to 13.2 (sd 11.8) in 2011/12 and the

11 mean years since the final diagnosis increased from 9.1 (sd 11.3) in 2000/1 to 11.5 (sd 11.0) in 2011/12 (Table 3). So to make this clearer in the discussion were have added (age stayed constant whilst the mean number of years since the first SMI diagnosis increased) to the sentence in question. 7. (Page 7, line 14-15) Would you expect your results to be the same as QOF SMI prevalence? Essentially GPs can decide what constitutes SMI to be added to their SMI register, so will tend to include patients beyond those with schizophrenia, bipolar disorder and other non-organic psychoses. QOF existed from 2004 (and no longer exists) so this may be the reason for the apparent increase in prevalence. Also, you have not shown that this increase is significant. As you note, QOF was introduced in 2004 so this may be the reason for the apparent increase in prevalence and we have noted this in the discussion For example, the lower rates in our study may be partly attributed to the exclusion of drug/alcohol induced psychoses, organic psychoses, dementia, uni-polar depression, personality disorders and psychotic disorders in childhood/ adolescence. Note that the QOF, although downsized, is still alive and mental health is still one of the incentivised conditions. The z-score from a comparison of 0.52 (prevalence in first year) and 0.63 (prevalence in last year) in a sample of 3,805,086 in the former and one of 5,069,748 in the latter would be a massive 328.9, when statistical significance at the 0.05 level would be indicated by a z-value of Since such comparisons would be irrelevant and non-informative in samples of this size (please see Lin MF, Lucas HC, Shmueli G. Too Big to Fail: Large Samples and the p-value Problem. Inform Syst Res 2013;24:906-17), we note in the discussion: However, the nature of the study was purely descriptive and we do not attempt to quantify associations. Since we did not have specific hypotheses about the variations in prevalence rates across deprivation quintiles or between SMI and control cases, and the potential comparisons are numerous, we refrained from testing for statistically significant differences instead focussing on the size of the prevalence rates and their apparent differences. Furthermore, statistical significance is less meaningful for datasets of this size. This is also addressed more clearly in the conclusion by emphasising that this is a descriptive study. 8. (Page 7, line 8-9) Sentences like A variable pattern of comorbidity was observed across different SMI subgroups and areas of high and low depravation do little to inform the reader what the results of this study are. Thank you for highlighting this point the tables and graphs are now highlighted so readers can see were to look. We have also expanded the results section and linked the tables and graphs so it s easier for the reader. 9. (Page 7, line 26) You suggest that increases in prevalence may be linked to increases in illicit drug use, but the reference does not show that there has been an increase in illicit drug use. Correction noted. This sentence has been deleted as it is speculative. 10. (Page 7, line 53) Because of your reporting of the data I am not sure there is an upward trend in comorbidity. This statement is based on the increasing trends across all comorbidities we measured over the study time period, which are summarised in Table 1. Overall, the mean number of comorbidities for a person with SMI was 0.6 in 2000/1 and 1.0 in 2011/12 which implies that the number of comorbidities almost doubled on average, over the time period we investigated. We are not sure what the reviewer means with because of your reporting of the data, but we are happy to address further if more details are provided.

12 11. (Page 8, line 6-9) This sentence doesn t quite make sense. Do you mean that the cost of comorbidity is greater than additive? We mean that the effects of comorbidity are not additive, i.e. if the cost for having condition A is X and the cost for having condition B is Y, the cost for having A and B is greater than X+Y. We have edited the text to make this clearer. 12. (Page 8, line 25) Your results are purely descriptive, so I m not sure that unmeasured confounding is an issue. We agree that it is less of an issue in this context but unmeasured confounding is not an issue for statistical tests only. For example, if we hadn t matched on age, SMI patients might have all been older or younger compared to the controls, hence our comorbidity estimates would have been confounded by age. Analogously, unmeasured quantities can confound the results from descriptive statistics. 13. (Page 8, line 25-26) Here you say you matched for depravation (at the practice level) but in the abstract you say you matched for practice. Which did you do? Thank you for pointing this out. We matched on practice, which implies deprivation as well since deprivation was measured at the practice level. We have edited the text to correct this. 14. (Page 8, line 28) I m unclear why you think obesity and smoking status may not be recorded accurately. Even ethnicity is pretty well recorded in CPRD. Ethnicity is recorded using Read codes and the last time we investigated in 2009 it was missing for over 70% of cases. Similarly we have seen varying degrees of missingness for BMI (between 5% in the latter years for relevant conditions e.g. diabetes, but it can be missing for up to 80% of patients in earlier years and for conditions for which weight is considered less relevant). Smoking status is recorded but the quality of the variable is questionable with patients quite often coded as never smoked when coded as smokers in previous years. In anyway, we have tried to explain better why such a matching would be irrelevant anyway. Please also see our first response to the first reviewer. 15. (Page 8, line 29-35) I think you are right not to perform a multitude of hypothesis tests, but this comes back to my earlier points about vague and multiple objectives and too much data to communicate. Some reporting of risk relative to the comparison group would not be inappropriate as otherwise what is the benefit of including this group? I agree that large data sets will give small P-values but this is not a reason to avoid any comparison. Also you are free to define your own significance level so this is not a major problem I you did which to test hypotheses. The data we report within the paper have been made clearer. Also please see our previous example regarding z-values and a test of proportions within this context. No matter how low the alpha level, the problem remains. We do not feel that the paper is misleading in anyway with its lack of p-values, and any such comparisons would have nothing to add (And we would be boringly reporting p-values <0.001 thought-out the paper). More importantly, we did not have specific a-priori hypothesis (which we state in the limitations section) and we wished for this to be descriptive groundwork to measure quantities associated with people with SMI (drugs and comorbidities). 16. (Page 8, line 35-37) I think this sentence needs restructuring. Do you mean that LSOA IMD of the GP practice is not a good proxy for individual level depravation? Is this important, given that you

13 are talking about the services the practice may provide? This is only a limitation if you were trying to use area IMD as a measure of individual level depravation. We mean that GP area deprivation will not necessarily be a good proxy for patient residence area deprivation, and evidence says that the relationship between deprivation and ill health may be underestimated (Individual level deprivation is beyond what is possible with databases work). We think it is worth mentioning because of the matching: if all people with SMI tend to live in more deprived areas compared to their matches within the same practice then we would have unmeasured confounding at work, although we hope that this is not the case. We have now rephrased the relevant sentence to make this clearer. 17. (Page 8, line 40-45) I worry that in this section you are proposing that any research into SMI using EHR is invalid because of difficulties around diagnosis. There is evidence that SMI recording is valid in primary care records, for example: Nazareth et al. (1993). Accuracy of diagnosis of psychosis on general practice computer system. Bmj, 307(6895), There is also evidence of diagnostic stability over time: Hardoon et al.(2013). Recording of severe mental illness in United Kingdom primary care, We are of the opinion that this work can be valid and is worthwhile. However, there are important limitations that need to be acknowledged, especially in this very difficult clinical area. In an accompanying paper that is under review we report that the diagnosis of SMI for a patient is not finalised in 20% of the cases within a year of first diagnosis (so for example a bipolar case might be later coded as schizophrenia). We do not think that our open reporting of the limitations (which would be acknowledged by all researchers in this area we feel) is making a disservice to us or this work. 18. (Page 8, line 51) I am unsure if these data show rising inequalities in the pattern and number of different comorbidities as this has not been tested. This is the same as point #10 we feel and has been addressed above. Again, comparing a mean of 0.6 to a mean of 1.0 in a sample of approximately 350 thousand people is non-informative. 19. (Page 8-9, line 55-4) I m unsure how the comorbidity results could be helpful in planning trials? Essentially trials need to be representative of the populations they are going to apply to. We have clarified this by rewording the final sentence: Multimorbidity is a possible confounding factor so will be important for planning intervention trials ensuring a that participants with SMI are representative regarding their morbidity burden and patterns of illnesses. Further Comments 20. Abstract (Page 2, line 40) inequalities rose for most conditions this is not clear, do you mean practices in the most deprived areas saw the biggest increase in comorbid conditions? This has been amended (as noted for reviewer 1 too) so that the meaning is clearer: and the gap between the prevalence of those with and without SMI increased over time for most conditions. 21. The results section of the abstract should probably report more numerical results (given that you have so many).

14 We appreciate that the abstract struggles to accurately report all details of the study. We have significantly revised and edited both the results and conclusion sections but we are limited to 300 words and it is impossible to fully report on all aspects of the study. 22. Introduction: (Page 3, line 33-41) This sentence is very long, and as a result is difficult to comprehend. Thank you for drawing our attention to this. The sentence has been split and amended: The factors that account for this include adverse effects of antipsychotic medication and unhealthy lifestyle behaviours which increase the likelihood of developing obesity, hypercholesterolaemia and metabolic syndrome, which in turn increase the risk of chronic diseases such as diabetes mellitus. Other barriers to the recognition and management of physical conditions include difficulty in understanding health care advice, reduced motivation to adopt new changes in lifestyle, poor compliance with treatment, cognitive deficits, reduced pain sensitivity (induced by antipsychotic medication), poor communication and social skills. 23. Introduction: (Page 3, line 51-52) There are longitudinal studies of comorbidity in SMI, and it is probably appropriate to refer to some of these. We agree there are other studies of comorbidity in SMI and do refer to these studies. We have now added one further study and edited the text to clarify how they are different to our study in the introduction. All these studies are also referred to in the discussion. 24. (Page 4, 1-4) Aim 1 could benefit from a full stop or being broken up into the multiple aims described. Thank you for spotting this this has been corrected and also relates to a comment picked up by the other reviewer. 25. Methods: (Page 4, Line 28-30) Is the consistent with the inclusion criteria for SMI registers group described here the Other SMI group in the tables? This should be clarified who are these people? Thank you for drawing our attention to this. As discussed throughout the paper we categorise as schizophrenia, bipolar disorder, affective disorder and other types of psychosis. We also provide the detailed codes we used to categorise cases into these four groups, which have been uploaded to We have also now made this clearer in the method section and clarified in the relevant column headings (table A5,6,7). Codes classified in the other types of psychosis group include Paranoid psychosis, Paranoid psychosis NOS, Psychosis NOS, Schizoaffective disorder, Nonorganic psychosis NOS. 26. Methods: (Page 4, line 54-55) As mentioned above the Methods section and Discussion sections have different definitions of frequency matching. Thank you, we have now edited and responded to this above. 27. Methods: (Page 5, line 2-3) IMD was elicited from the practice postcode. I m unclear how you did this as a different measure of IMD is used in Scotland which does not map onto IMDs for

15 England. It would be helpful to the reader if this was described more fully, including an overview of what IMD captures. This is a technical CPRD issue and thank you for bringing this to our attention so we can clarify. We have now edited the other socio-demographic characteristics section briefly to clarify that a different measure is used within each country and the deprivation the CPRD is reporting for each of its practices (and the deprivation quantile it ends up being allocated do) is determined by the deprivation within the specific country, not the whole of the UK. Consequently, an average deprivation practice in Scotland will be in a more deprived area compared to an average deprivation practice in England. Results 28. Methods: (Page 6, line 21-24) The sentence Notable exceptions were coronary heart disease and heart failure; rates fell for both groups, as well as stroke, rates remained relatively stable for the SMI group but fell for controls does not read well. Thank you for spotting this. This has now been revised: There were some notable exceptions: the rates for coronary heart disease and heart failure fell for both groups and the rates for stroke remained relatively stable for the SMI group but fell for the controls. REVIEWER REVIEW RETURNED GENERAL COMMENTS VERSION 2 REVIEW Susan Smith RCSI Dublin Ireland 02-Sep-2015 Thank you for addressing my suggestions and comments. The manuscript still needs some copy-editing. Fro example, page 9, lines do not make sense. BMJ Open: first published as /bmjopen on 15 December Downloaded from on 17 March 2019 by guest. Protected by copyright.