Commentary on RSD focus article

Beginning

Whenever two or three pain doctors are gathered together there is a high probability that the conversation will drift to reflex sympathetic dystrophy (RSD). I think the reasons are that we all see RSD patients, that there is a tantalising link between our needle therapies and improvement, and that in the absence of evidence opinion holds sway - ideal fertile ground for conversation.

Tanelian's focus article highlights some of the areas of ignorance:

what causes RSD?

what is the natural history?how best should it be managed?

This paper will take these three points briefly and then explore the wider ramifications of how we should approach clinical research into this and other pain conditions, pursuing Tanelian's digression into placebo.

WHAT CAUSES RSD?

The IASP definition of "continuous pain in an extremity after trauma which may include fracture but does not involve a major nerve, associated with sympathetic hyperactivity" together with its rider is a succinct and thoughtful description of the problem. The presence of sympathetic hyperactivity can be demonstrated with greater or lesser ease. The problem is that the presence of sympathetic hyperactivity has been taken to mean that sympathetic hyperactivity causes RSD. This is akin to saying that it is dark outside and the street lights are on, therefore the street lights have caused the darkness. As a buttress to the argument that sympathetic hyperactivity causes RSD it is argued that sympathetic blockade cures RSD, therefore sympathetic hyperactivity must have caused the RSD. This is a false syllogism because, as Tanelian points out, the evidence that sympathetic blocks cure RSD is far from strong. Patients may improve after treatment which includes sympathetic blockade, which is splendid, but there is no proof that it is the sympathetic block rather than a change from disuse to use of the limb which has effected the change.

The answer to the question "what causes RSD?" is that we do not know. Why don't all patients with a Colles' fracture develop RSD?, or why, if all patients have an injury response which could go on to develop into RSD, do only some patients present with the syndrome? There is an obvious analogy to pains which persist after surgery. A proportion (?1%) of patients develop pain after herniorrhaphy. As with RSD we do not know what is different about these particular herniorrhaphy patients, and why they go on to develop persistent pain when their peers do not.

WHAT IS THE NATURAL HISTORY?

Once more the answer is that we do not know. Tanelian quotes Subbarao and Stilwell' audit [Subbarao and Stilwell, 1981] that, fourteen months after their last treatment, two-thirds of 125 RSD cases had retired, were officially disabled or did not return to the same job. This was despite the physicians reporting 51% as having excellent or good response 2.5 months after treatment. It suggests strongly that benefit of the treatment did not always persist and that this is not always a self-limiting disorder.

Tanelian discusses the oft-quoted contention that results of early treatment will be better than those when the pain is treated late. If there is an element of self-limitation in RSD (the one-third of the 125 cases who had not retired or had to change their jobs), then early treatment may claim as cures those who would have improved anyhow. The unknown is the extent to which early treatment could cure those who would otherwise have had pain of long duration. The Subbarao and Stilwell audit does not help to answer this question.

Our ignorance of the natural history means that any comparison of treatment intervention must be organised, for instance by stratified randomisation, so that duration of the syndrome among the patients in each treatment group is balanced. Testing a magical new cure on 'early' RSD patients and comparing it with standard treatment on long-standing RSD patients might well give a misleading answer.

HOW BEST SHOULD RSD BE MANAGED?

One way to approach this question is to turn it around and ask what constitutes a good clinical result, for the patient and for us. The simple answer is that function of the limb returns to normal, and that pain disappears. There is a catch here - which is the most important outcome, restoration of function or disappearance of the pain?, or are both equally important? For the design of future treatment comparisons we need to plan the outcome measures more carefully, to allow for the fact that we may get different answers for function and for pain.

Tanelian's focus article provides a huge number of studies of treatments for RSD in Table 1. It is not clear whether or not he has looked at the full deck of cards ("I have reviewed the majority of studies cited in Medline"). He cites reasonable criteria for study validity, five out of the six quantitative diagnosis of RSD, cross-over design, randomisation, prospective, double-blind and placebo-controlled. He does not tell us how many of the studies in Table 1 meet these criteria, although we could work it out for ourselves. Most importantly there is no qualitative or quantitative attempt to pull this data together and to give us a clinically useful conclusion. Instead he chickens out, and says "Having reviewed the literature, I agree with the conclusion Betcher reached in 1953 ... "(that) sympathetic blockade is a beneficial means to reduce pain and thereby allow patients to conduct physical therapy, and resolve their manifestations of RSD".

The process pundits would argue that this is not a valid systematic review [Mulrow, 1987]. We are not told how hard the author pushed to obtain his citations, or his search strategy or whether or not he pursued citations in the reference sections of the articles he identified. There is no judgement presented of the quality standards of the articles identified. He has included non-randomised studies in the Table despite his mention in the text of the fact that non-randomised studies can lead to overestimation of therapeutic effect of up to 40% [Schultz et al, 1995]. If this reads like harsh criticism it is only because I really want to know the answer, and what shines through is that we do not have the randomised studies we need to provide such an answer. My concern is that by quoting the non-randomised studies we perpetuate the current state of ignorance. Only by admitting that ignorance can we move forward, declare a research agenda and set about the design and execution of the studies required to fulfil the agenda.

The way forward

What we really want to provide is interventions which break the cycle of inability to use the limb. We can (to an extent) help with the pain, but we want to reverse the disuse if possible. If needle interventions ,such as sympathetic blocks, from intravenous regional to stellate to lumbar sympathetic, can achieve this aim then that is marvellous. What remains unclear is whether sustained reversal is possible, in which patients if not all can this be achieved, and what it takes to achieve the reversal. This is very close to Tanelian's quote from Betcher "sympathetic blockade is a beneficial means to reduce pain and thereby allow patients to conduct physical therapy".

We do need to be sure that our blocks do not make things worse. We need the simplest and safest procedure to achieve our goal. If local anaesthetic can achieve the facilitation of physical therapy then we should be using local anaesthetic rather than neurolytics, because local anaesthetic is safer. If more sustained block is required would local anaesthetic infusion be more sensible than neurolytics?

DESIGN OF STUDIES

Studies in this field, as in others, need to be randomised to minimise selection bias. Ideally they should be double-blind, although this may be logistically difficult to organise for needle interventions. They need to be of adequate size to have the power to tell us that a negative result is a true negative. This would be buttressed by including in the design an active control known to work in the condition, so that we would know that the investigators could distinguish that active control from either the test treatment or a negative control (placebo). Unfortunately in RSD, as in many other conditions, there is no clear candidate as standard treatment to act as an active control.

The outcome measures need to include function as well as pain. Ideally they should include a dichotomous clinically intelligible component, like the time-honoured "Is your pain half gone?". Follow-up needs to be at least a year, judging from the data which Tanelian quotes.

None of this is easy. Tanelian helpfully includes Table 2 and text to indicate that the numbers of patients required to answer these questions are substantial. Such calculations require making a guess at the placebo response. A core problem here is that we do not know the natural history. Some of these patients will get better despite the treatment. Tanelian quotes a conservative estimate of the placebo response as 35%, while saying that many studies report rates which are higher.

As part of a series of systematic reviews on neuropathic pain treatment [McQuay et al, in press] we have used L'Abbé plots to try to pin down the variability in trial results due to just this phenomenon of 'success' (pain relief) in the control groups [L'Abbé and Detsky, 1987]. Each trial is a point on the scatter plot, using the success rate with the intervention under test (Experimental Event Rate, EER; y axis) and the success rate in the control group (Control Event Rate, CER; x axis). The point for a trial in which the test treatment proves better than the control will be in the upper left of the graph, between the y axis and the line of equality. If test is no better than control then the point will fall on the line of equality.

The Figure shows results from trials of both antidepressants and anticonvulsants in diabetic neuropathy [McQuay et al, in press]. The most important feature to notice when thinking about future RSD studies is that the CER, the event rate in control groups, varies enormously, even when trials are showing similar levels of efficacy in the EER. This means that calculating sample size from a fixed CER of say 35% may grossly underestimate the numbers required.

GETTING A GRIP

Few of us sees enough RSD patients each year to mount studies of adequate size which will complete within our working lifetimes. The way forward has to be multi-centre studies which follow the design feature outlined by Tanelian and above, perhaps organised under the aegis of APS. Which question should we tackle first?

References

L'Abbé KA, Detsky AS. Meta-analysis in clinical research. Ann Intern Med 1987; 107:224-33.

McQuay H, Nye BA, Carroll D, Wiffen PJ, Tramèr M, Moore RA. A systematic review of antidepressants in neuropathic pain. Pain (in press)

McQuay H, Carroll D, Jadad AR, Wiffen P, Moore A. Anticonvulsant drugs for management of pain: a systematic review. British Medical Journal 1995; 311:1047-52.