Effectiveness of a symptom-clinic intervention ... multiple and persistent physical symptoms, 2024, Burton, Deary et al

[Hutan]

Diagnosis

Eligible participants were adults aged 18–69 years with multiple and persistent physical symptoms as evidenced by a Patient Health Questionnaire-15 (PHQ-15)20 score between 10 and 20. This score represents moderate or moderately severe symptom burden.

See the post upthread for the list of questions in the PHQ-15. I note that women have to answer an additional question about periods, and I think most menstruating women would answer at least 'bothered a little' about period symptoms. So, the PHG-15 and the diagnosis approach makes it more likely that women will be included in the sample.
Edit - later in the paper they say they adjusted scores when people left that line and/or the one about sexual activity blank.

To be eligible, individuals were required to have at least one code for a syndrome defined by physical symptoms, such as irritable bowel syndrome or fibromyalgia, in their GP electronic health record and to have been referred to specialists at least twice in the preceding 36 months (later extended to 42 months due to pandemic lockdowns). Exclusion criteria were evidence in medical records of previous or current major illness likely to cause symptoms, inability to manage personal care or leave the home independently, substantial thoughts of self-harm (ie, a score of 3 on the self-harm question of the Patient Health Questionnaire-9 [PHQ-9]; appendix pp 73–74), difficulty conducting a health-care consultation in English without either a professional or family interpreter or other assistance, current pregnancy or pregnancy within the past 6 months, and currently undergoing specialist rehabilitation or psychological therapy.21

So, they were looking for people who had a code for a physical symptoms syndrome, had been referred to specialists at least twice in the preceding 3 or so years, but did not have a medical diagnosis thought to cause symptoms. That leaves a great gaping hole for people with persistent symptoms with a biological cause that has not yet been identified. And these researchers thought it was ethical to instruct doctors to 'negotiate' a made up explanation basically amounting to 'your brain is wrong, it got muddled up somewhere along the way, and so you only think you are unwell, but actually you are fine, so, get on with things'.

Participants were recruited in four stages. First, GP practices did a structured search on their electronic health records to identify potential participants on the basis of diagnostic and referral codes. The results of these searches were checked by a GP within the practice to avoid sending invitations to people for whom it would be inappropriate, including those for whom the GP believed symptoms were more likely to be attributable to an underlying medical condition.

GPs were able to veto someone being invited into the study. I'd be very interested to see the gender split on the veto'd versus non veto'd.

Second, practices sent a trial-participation invitation and information pack to people identified via this search. This pack contained the participant information sheet, a PHQ-15 questionnaire, and a reply form to be sent to the trial team.

Depending on what the patient information sheet said, there may have been some substantial self-selection. It would be interesting to know how the intervention was described.

 

[Hutan]

Randomisation; masking
A big deal is made of randomised allocation of people to the treatments. But that is rather insignificant when the participants knew whether they were allocated to the active treatment or 'nothing'.

Due to the nature of the intervention, masking participants to whether they were in the intervention group or in the usual care only group was not possible. The processes and timing of outcome collection were identical across both groups and were done by staff at the Clinical Trials Research Unit (including JW), who were masked to allocated group. Statistical analysis was done masked to treatment allocation.

Purposive sampling ensured a mix of participants who were currently working or not working and those with different predominant symptoms (eg, pain or fatigue).

Just noting that quote about some interviews of participants they did - the trial did include people whose primary symptom was fatigue. I guess if ME/CFS isn't diagnosed, you don't have to follow the NICE ME/CFS Guideline.

They audio recorded all the symptom clinic consultations. That will be a gold-mine as they refine techniques to convince people their symptoms can safely be ignored, and if ignored well enough, will go away.

We used participant-reported outcome measures completed at 13 weeks, 26 weeks, and 52 weeks after randomisation via posted paper forms.

A lot of measures were taken - it will be interesting to see if results for all of this are reported on:

The PHQ-15 ...Data for age, ethnicity, first language, education, 5-Level EuroQol-5 Dimension (EQ-5D-5L) score,24 European Health Literacy Survey-6 (HLS-EU6) score, 25 ICEpop Capability Measure for Adults (ICECAP-A) score, 26, Patient Global Impression of Change (PGIC) score, PHQ-9 score, Patient-Reported Outcomes Measurement Information System–Ability to Participate in Social Roles and Activities (PROMIS-APS) score,27 Short-Form 6-Dimension (SF-6D) score, 28 Short-Form 12-Dimension (SF-12) physical component summary score, SF-12 mental component summary score, and Somatic Symptom Disorder–B Criteria Scale (SSD-12) score 29

 

[Hutan]

The primary outcome was self-reported PHQ-15 score 52 weeks after randomisation, analysed by intention to treat.

Secondary outcomes were quality of life (ie, via EQ-5D-5L, SF-6D, and ICECAP-A), depressive symptoms (ie, via PHQ-9), anxiety symptoms (ie, via General Anxiety Disorder-7 [GAD-7]),30 ability to participate in social roles and activities (ie, via PROMIS-APS), PGIC, and health-care use. Health-care use was assessed via a self-report form to obtain data during the 52-week period in both primary and secondary care (appendix pp 137–140). We also included the HLS-EU6 measure of health literacy and the SSD-12 measure of the psychological burden of physical symptoms.

We considered potential harms in terms of adverse events (with a particular focus on delayed or emerging diagnoses of serious medical conditions), withdrawals in the intervention group indicating dissatisfaction, and missed opportunities for timely diagnosis through a reduction in diagnostic testing behaviour by GPs of participants in the intervention group. Adverse events were mainly identified through participant-reported outcome measures during scheduled collection of outcomes, but GPs with an extended role were required to report adverse events to CM, the trial manager, if they were detected during symptom-clinic consultations as well.

It looks as though harms were reported by participants, but I assume that if the participants stopped participating and weren't contactable, then the harm wouldn't be reported. There is no indication that medical records were checked during that following year or that there was any feedback from the participant's own GP, and health care use was only gathered by self-report from the participants who remained around to still be participating.

Outcomes were analysed with partly nested, heteroscedastic, mixed-effects regression models.34, 35 These models included fixed effects for baseline participant-reported outcome measure scores, gender, age, and allocation and random effects for the GP with an extended role in the intervention group only.

I always get a bit worried when investigators start messing around with the data. Does this mean 'Oh, this doctor didn't seem to have such a good impact on improvements as all the other doctors, so we will improve the scores of his patients a bit'? Or, older people didn't seem to improve as much as younger people, and our treatment sample had more older people than the control sample, so we'll just improve the results of all old people. It seems like a black box of opportunities for data manipulation in the direction you want. I think the onus should be on researchers to make the control group a good match so adjustments aren't needed. And I don't understand the rationale for adjusting for the impact of the individual doctors 'treating' the participants.

Analyses followed the intention-to-treat principle and no adjustments were made for multiplicity. Variation in the effectiveness of GPs with extended roles was quantified with the intraclass correlation coefficient from regression models.

Numbers needed to treat to benefit were calculated post hoc via the reciprocal of the difference between the probabilities of a change of each magnitude; these effect sizes were multiples of minimal clinically important differences (MCIDs) for change from baseline in both groups from logistic-regression models adjusted for GP with an extended role in the intervention group only, baseline PHQ-15, age, gender, and effects of the intervention.

Ugh

 

[Hutan]

7837 people identified from GP records
891 excluded or not sent a participation pack - mostly due to the GP saying they aren't suitable e.g. because their symptoms probably are due to a real disease, probably also some GPs would know some patients would not be receptive

6946 sent the participation pack
5688 did not return the pack!!
1258 assessed for eligibility

904 were excluded, due to not being eligible or not wanting to proceed

354 randomly assigned to the treatment or control. That's about 5% of both the people identified from GP records and of the people sent a participation pack. There is such a selection bias there. If this treatment turned out to be wildly successful in this patient group, that selection bias would need to be borne in mind - this trial would not be evidence of the intervention being successful in the vast majority of cases.

 

[Nightsong]

When disproportionate to detectable physical disease or representing so-called functional disorders, they constitute approximately a third of referrals from general practitioners (GPs) to specialists in the UK. [1]

This reference is to Nimnuan et al. Medically unexplained symptoms: an epidemiological study in seven specialties; I had a brief skim of this paper. Initial thoughts:

MUS definition was based on absence of a "conventional biomedical explanation" 3 months after routine examination & investigations. HADS to detect anxiety/depression; no structured interviews. They not only did not find associations between MUS and depression/anxiety (as measured by HADS) or work status which seems to contradict a great many other psychosomatic papers and they do not really address why physical but not psychological attributions would not be similarly associated. The sample size and response rates were lower than expected. Some results achieve statistical significance but look like weak associations or with wide CIs; no correction for multiple comparisons. The %MUS figures seem high and there is also a high variability: the highest in gynaecology (66%) and the lowest in dental (37%). 45% in rheumatology, 53% in cardiology, 58% in gastroenterology, 62% in neurology - these seem very high. Additionally the authors developed novel tools for symptom review and illness cognition but there was no detailed discussion of their psychometric properties.

 

[Hutan]

Of the 354, 176 were assigned to usual care and 178 to the intervention
135 assigned to usual care made it to 52 weeks; 144 in the intervention made it to 52 weeks.

The numbers used in the Intention to Treat Analysis were those still present at 52 weeks, so did not include people who withdrew or were lost to followup. Numbers who withdrew and were lost to followup were similar in both groups and not very large; more withdrew in the control group.
3 of the people in the control group did not have baseline data; presumably that was imputed from their 3 month data.

To deliver the intervention, we initially recruited and trained seven GPs. However, two dropped out early on, one before seeing any participants, because of other commitments, so five GPs with an extended role provided the intervention.

That's interesting. So, one GP dropped out with no reason given and had seen some participants, and there is nothing said about what happened to their patients and the data.

Of the 354 participants, 291 (82%) identified as women and 63 (18%) identified as men.

As expected.

According to the HLS-EU6 survey, at baseline, only 122 (35%) of 354 participants met the cutoff for “sufficient” health literacy, 167 (47%) had scores in the range suggesting “problematic” health literacy, and 50 (14%) had “inadequate” health literacy

All the better to (tr)eat you... (reference to the wolf in red riding hood)

 

[Hutan]

so in a subjective measure in an unblinded study comparing a group that got something to a group that got nothing, they achieved the bare minimum that could be conceivably called clinically important.

Well yes, and even then 'conceivably' is doing a lot of heavy lifting. As @rvallee would say, the giant spaghetti monster in the sky is conceivable, it doesn't mean it is likely.

As Nightsong said the Toussaint paper suggested the standard error of measurement was 2.3, which seemed to be suggesting that that was an estimate of a minimal clinically important difference:

Here's a PDF for the Toussaint et al paper: link - the SEM was 2.3 for the PHQ-15m. The adjusted between-group difference was -1.82 (95% CI –2.67 to –0.97), which although statistically significant (p<0.0001) does not meet that MID for clinical significance.

And this paper found an improvement of 1.82. So, that's not actually clinically important. But they argued that because the 95% confidence interval of -2.67 to -0.97 includes the minimal clinically important difference, they could still say their intervention helped.

So, I would say 'in a subjective measure in an unblinded study of highly selected individuals that cannot be assumed to be representative of the disease population, comparing a group that got something to a group that got nothing, and with some dropouts and who knows what they did with their model "adjustments", even then, they did not achieve the bare minimum that could be conceivably called clinically important.'

 

[Hutan]

And this paper found an improvement of 1.82. So, that's not actually clinically important. But they argued that because the 95% confidence interval of -2.67 to -0.97 includes the minimal clinically important difference, they could still say their intervention helped.

I think, just assuming a normal distribution with that mean and that 95% confidence interval, that there is a 13% chance that the true mean is the supposed clinically important difference of -2.3 or more. Which makes sense if you look at the reported 95% confidence interval of -2.67 to -0.97. -2.3 is well to the end of the range. A question for people with better statistics knowledge than me, (ignoring all the other problems with this paper and just looking at the maths), can the researchers credibly claim that this study shows that the intervention achieves a minimal clinically important difference?

If you set that along side the harms that they have not properly assessed and the cost of providing the intervention, I think there is a lot of smoke and mirrors and no real benefit.

The authors seem to be suggesting that, for the people it works for, it works really well. I haven't seen the data on that yet.

 

[Hutan]

Results

There were people who didn't attend the initial session or stopped attending the sessions, and that will probably have affected the results, but the rates of participation (for the 4 sessions) aren't too bad.

Of the 178 participants who were randomly assigned to the intervention group, 165 (93%) attended the initial consultation, 156 (88%) attended the initial consultation plus at least one follow-up session, 143 (80%) attended the initial consultation plus at least two follow-up sessions, and 122 (69%) attended all sessions. None of the 13 participants who attended only one follow-up session completed the second PSYCHLOPS measure but 13 (62%) of the 21 participants who stopped after two follow-up sessions completed it. There were 24 unmasking incidents—15 (63%) were definite and nine (38%) were probable—across 816 participant outcome-data collections.

At baseline, PHQ-15 scores were 14·9 (SD 3·0) in the group receiving usual care and 15·0 (2·9) in the group receiving the intervention (figure 3). At the primary-outcome point of 52 weeks, PHQ-15 scores were 14·1 (3·7) in the group receiving usual care but had reduced to 12·2 (4·5) in the group receiving the intervention. The adjusted between-group difference of –1·82 (95% CI –2·67 to –0·97; table 2; appendix pp 19–21) was statistically significantly in favour of the intervention group (p<0·0001).

No statistically significant difference at 13 weeks or 26 weeks.

Table 2 gives the means for a range of other measures at 52 weeks, for the two groups. It is concerning that the numbers of participants varies quite a lot for each measure - missing data creates opportunities for inconvenient results to be lost. There is no analysis of statistical significance or minimal clinically important difference. There is no comparison with baseline measures. There is no discussion of these other measures in the results section at all.

Here's one: PGIC Patient Global Impression of Change
Usual care 1.8
Intervention 3.2

The Patient Global Impression of Change scale is a single, self-administered question asking respondents to rate how their condition has changed since a certain point in time. This protocol was validated in individuals aged 18 years and older who were being treated for chronic pain.

Since the start of the study, my overall status is:
1 [ ] Very Much Improved
2 [ ] Much Improved
3 [ ] Minimally Improved
4 [ ] No Change
5 [ ] Minimally Worse
6 [ ] Much Worse
7 [ ] Very Much Worse

It therefore looks as if the usual care people were reporting that their health had, on average, 'much improved' tending to 'very much improved, while the intervention people reported that their health had, on average, 'minimally improved' tending to 'no change'. I find that hard to believe, and I wonder if data got entered in the wrong columns. But, it's either not reflecting well on the utility of the intervention or it's not reflecting well on the reliability of the paper.

I'd appreciate it if someone could check that PGIC finding. It might be worth poking around in the other data there.

Complete self-reported health-care use data were available for 166 (47%) of 354 participants, 77 in the intervention group and 89 in the group receiving usual care. There were only minor differences between groups in primary-care contacts, outpatient referrals, and diagnostic investigations (appendix pp 21–22).

A very low percentage of participants reported their health-care data. I haven't looked at the differences between group, but the authors are suggesting that the differences are minor.

On adverse events - some of the participants turned out to have medical conditions that may have explained their 'persistent physical symptoms'.

There were 39 adverse events in the group receiving usual care and 36 adverse events in the group receiving the intervention (appendix p 22). There were no statistically significant between-group differences in the proportion of participants who had non-serious adverse events (–0·03, 95% CI –0·11 to 0·05) or serious adverse events (0·02, –0·02 to 0·07). The serious adverse events included one participant diagnosed with cancer, identified through routine screening; one participant with a history of irritable bowel syndrome who developed cholecystitis; and one participant who had a small pituitary adenoma found on imaging done due to dizziness.

 

[Lucibee]

this paper found an improvement of 1.82.

It found a *between-group* difference of 1.82.

The median scores at baseline in both groups were 15 - but also need to consider that entry criterion was a score between 10 and 20. They excluded those with high (20-30) or low (0-10) scores.
This improved (on average) at 52 weeks to 14 in the usual-care group (1 pt diff), and to 12 in the ignore-your-symptoms group (3 pts diff).

Studies like this should be banned.

 

[Lucibee]

This makes me so cross!

What I'd like them to have done is to maybe do a trial where they use their "intervention" as the placebo control, and do some proper work-up and investigation in a true intervention group.

But the problem is always going to be, unless they actually find out what is wrong and treat it, there will likely still be little difference between the two groups.

It's a very sorry state of affairs.

 

[Hutan]

It found a *between-group* difference of 1.82.

yes, sorry if it wasn't clear. Improved relative to the outcome in the 'do nothing' group.

 

[Lucibee]

I'd appreciate it if someone could check that PGIC finding. It might be worth poking around in the other data there.

In the appendix (pdf link: https://www.thelancet.com/cms/10.10...92cea412-1aa4-4f3b-82d5-0b3e51d62615/mmc1.pdf), they have the scale the other way around: "0= No change or condition has got worse; 7= A great deal better"

But the form itself is very confusing, because the two scales seem contradictory.

It looks like they've reported the top half of the scale, and not the bottom likert bit.

tbf - that also seems to match the data they got from the PHQ-15 pretty well (as can be seen in the full results plot).

 

[rvallee]

All things considered, this looks a lot like the FINE trial. Definitely, trials like this should be banned. They have zero legitimate value and make a mockery of science.

I tried to find what they mean by negotiating symptoms. There's nothing about it. About explaining symptoms, the model is supposed to be shown in Figure 1, but that graphic is literally just a dot. Which is oddly fitting. I guess they forgot to add it.

This reads like all the junk techno buzzword you hear from business suits who understand nothing of the underlying technology but are used to BS their way around marketingspeech:

The symptom-clinic intervention was delivered by GPs with an extended role, whose work typically uses the skills of holism and of managing complexity and uncertainty, which are central to generalism

The skills of "holism", which is obviously not a skill, and whatever the hell generalism means, it clearly doesn't apply to making stuff up and convincing people of things that are false. One interpretation would be of general intelligence, but this isn't it at all. In fact this makes a mockery of true general intelligence, which scoffs at small-minded nonsense like this. This is shady salespeople techniques, nothing more.

Isn't statistically significant but not medically significant supposed to not matter? In their conclusions they report that it's only statistically significant and further research should, as is tradition, evaluate cost-effectiveness. But it's not clinically significant, a bar that is clearly set way too low anyway, so it can't be cost-effective, by definition.

From a cited paper on what they mean by a "rational" explanation, another Burton paper:

(1) it is plausible (to both doctor and patient; (2) it does not imply weakness or fault on the part of the patient; (3) it promotes therapeutic partnership or action; (4) it applies a descriptive label (which need not be a specific diagnosis); (5) it addresses causation, although this may be through perpetuating mechanisms rather than root cause; and (6) it is created through dialogue between doctor and patient

And of course that's total BS. They're sort of "elevating themselves by their own bootstraps" here.

What decades of never having to make sense does to people's reasoning skills. Even medieval alchemists would find them pedestrian.

 

[Lucibee]

If Symptoms Clinics improve patient well-being and reduce the need for tests they will be popular with health services and patients.
We believe it is important to test the Symptom Clinic to see whether it should be made widely available.

£1.5million spent on this (https://www.dev.fundingawards.nihr.ac.uk/award/15/136/07)

This is the protocol paper: https://www.ncbi.nlm.nih.gov/pmc/articles/PMC9668014/

But I'm having trouble finding out exactly what "The Symptoms Clinic" does in the 90-110 minutes it has of a patient's attention.

The two cited studies for the Symptoms Clinic in the protocol are these:

1. Morton L, Elliott A, Thomas R, Cleland J, Deary A, Burton C. Developmental study of treatment fidelity, safety and acceptability of a symptoms clinic intervention delivered by general practitioners to patients with multiple medically unexplained symptoms. J Psychosom Res 2016;84:37–43. 10.1016/j.jpsychores.2016.03.008 [PubMed] https://pubmed.ncbi.nlm.nih.gov/27095157/

2. Burton C, Weller D, Marsden W, Worth A, Sharpe M. A primary care symptoms clinic for patients with medically unexplained symptoms: pilot randomised trial. BMJ Open 2012;2:e000513. 10.1136/bmjopen-2011-000513 [PMC free article] [PubMed] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3330253/

The most they provide is this:

The consultations were structured to first hear the patient's experience of illness then to propose and negotiate constructive explanations of physical symptoms. These explanations were used as the basis for simple cognitive and behavioural actions to modify symptoms and their impact. No specific attempt was made to screen for common mental disorders; however, patients were encouraged to describe their emotional responses to symptoms and other events, and diagnostic labels such as depression were discussed collaboratively with the patient rather than imposed by the doctor.

Although I suspect this study provides more details (ref 19 in the main paper): https://pubmed.ncbi.nlm.nih.gov/37441925/ ... eta - yes it does - full open access version here: https://www.sciencedirect.com/science/article/pii/S0738399123002501?via=ihub

 

[Hutan]

In the appendix (pdf link: https://www.thelancet.com/cms/10.10...92cea412-1aa4-4f3b-82d5-0b3e51d62615/mmc1.pdf), they have the scale the other way around: "0= No change or condition has got worse; 7= A great deal better"

But the form itself is very confusing, because the two scales seem contradictory.

It looks like they've reported the top half of the scale, and not the bottom likert bit.

Thanks Lucibee.

It looks as though they have completely changed the way the PGIC is scored, as well as using two different methods of collecting scores. And even then, the intervention doesn't come out well. Bear with me, it's confusing, and I hope I haven't confused myself. But, if I haven't, then it confirms my impression of the work of these people - it would be a joke if it didn't have an impact on people's lives.

PGIC - Patient Global Impression of Change - so it's an important measure

Here's the approach I found when googling PGIC:

PGIC Patient Global Impression of Change
Since the start of the study, my overall status is:
1 [ ] Very Much Improved
2 [ ] Much Improved
3 [ ] Minimally Improved
4 [ ] No Change
5 [ ] Minimally Worse
6 [ ] Much Worse
7 [ ] Very Much Worse

And that's fair enough, there is the full range from very much improved, right through to very much worse. A low value is good.


But the top part of the PGIC that is reported in this study's appendix, as copied in Lucibee's post above, reverses the order:



But look - the range is essentially only from 'no change' to 'wonderful'. And, they don't say how that scale is scored. I reckon just that scale alone sums up all the problems with the psychosomatic medicine proponents. But, incredibly, these authors have managed to add layers of obfuscation and confusion to that.



The second scale in the PGIC scale appendix does have the full range:


But that is a 10 point scale, and it runs from better to worse, so lower numbers are better.


It's all a mess - we don't know what scale was actually used.

To remind ourselves of the numbers that were reported in this study for PGIC:
Usual care 1.8
Intervention 3.2

So, if the bottom scale in the appendix was used, the average outcome reported by the usual care people was better than the average outcome reported by the intervention people. !!

If the top scale in the appendix was used and a logical scoring symptom running from low to high was used, from 1 to 7, the average intervention score of 3.2 is still 'A little better, but no noticeable change'.

 

[Trish]

Maybe write to the authors and ask how the figure was calculate. They shouldn't be reporting a figure without the clear source.

 

[Trish]

How can something be 'a little better but no noticeable change'? If the change isn't noticeable, how do they know it's a little better?
That scale that only allows one negative/no change and lots of variations of positive should be illegal. It's not a research instrument, it's the cheats version of market research.

 

[Lucibee]

@Hutan It looks like they've used the upper portion of the scale - which should be graded 1-7.

Table 9.2 has a typo - saying that it scores 0 to 7 in the right hand column. But it's clear from the questionnaire itself that 1 should be "No change (or worse)" and 7 = "A great deal better" because there are only 7 items.

If table 6 is correct, the intervention can only be superior if they've used this upper scoring method. So the bottom scale is superfluous.

That's fine. It agrees with graph of the scores for PHQ-15.

So on that scale, 1.8=Almost the same, hardly any change (usual care), and 3.2=A little better, no noticeable change (intervention).

But they should have said so in the main paper that this was the case, because it looks a lot less rosy.

 

[Hutan]

@Hutan It looks like they've used the upper portion of the scale - which should be graded 1-7.

So on that scale, 1.8=Almost the same, hardly any change (usual care), and 3.2=A little better, no noticeable change (intervention).

Yes, that looks right.

There are different versions of the PGIC. I don't understand how any scientist could look at the version these authors used (the version above) that so obviously minimises declining health and any harm from the intervention and has vague, difficult to differentiate descriptions and think that it was ok to use. It suggests that all of the literature using the PGIC is suspect until proven otherwise.

P.S. even the instruction on the questionnaire serves to underline to the people in the 'care as usual' group that they didn't get care at the special clinic, and so leads them to a default of 'no change'.