Please insert each new comment in a new row.

Despite at times being courageous in taking a sceptical approach to the evidence, there are still serious problems and biases.

Do people really still believe that the mechanism of action of antidepressants is ability to block synaptic reuptake of monoamines? Surely it is better seen as a theory which has outrun its usefulness. It is clearly at least too simplistic. Most psychopharmacologists have given it up - it is about time clinicians did as well, so that the pharmaceutical industry cannot quote them in defence of yet more me-too drugs.

Thank you. We have amended the text

The reference to Fonagy (2003) is idiosyncratic and merely his opinion. Surely the reason that there are so many psychological therapies for depression is that it is common and there is a natural tendency to prefer short-term treatments over psychoanalysis.

Thank you for this comment

The arbitrary nature of the steps in the model may need emphasising - in practice there is much more overlap eg. should mental health specialists only treat resistant and recurrent depression? Can primary care really cope with all moderate and severe depression? There is a need for at least some flexibility in the model and this could be emphasised to avoid rigid overinterpretation. WHO has produced useful guidelines about the balance between primary and secondary care - should these be mentioned?.

Thank you -we have revised the stepped care framework in light of this and other comments.

The arbitrary nature of the definition of clinical significance may need to be emphasised, unless more explanation can be given of the reason for choosing RR<0.8. Such a definition is not used elsewhere in the literature, as far as we know. The difference between mean change scores (active treatment versus control) is probably the most reliable method of assessing the clinical significance of active effects (see below). It may need to be emphasised that measures of mean endpoint and mean change scores are usually made on the same or similar data - if the report wishes to continue with such a definition of clinical significance it needs at least to clarify why one method should be regarded as producing clinically significant results whereas another does not.

The GDG took advice, and 0.8 seemed like a sensible rule of thumb; RR were always interepreted with their 95% Cls

Although the report mentions the bias in drug trials through unblinding, no mention is made of the fact that psychotherapy trials cannot strictly speaking be conducted double-blind. To provide a balance in the discussion between the data on pharmacotherapy and psychotherapy, there needs to be information about the problem of adequacy of control groups in psychotherapy trials. This also applies to trials of other treatments, such as exercise, discussed in section 5. Psychotherapy trials may well be as biased as drug trials.

Thank you -.We have amended the section on issues in RCTs

Some mention should be made of the long-term nature of psychotherapy. Besides making it difficult to conduct clinical trials over a long period of time, long-term treatment may have more lasting benefits. There does need to be some counteracting of the tendency towards evidence reinforcing short-termism in treatment. Although such short-term effects are easier to measure, they are at least considerably compounded by placebo effects. Long-term psychotherapy is not necessarily ineffective just because it is difficult to measure its effects.

Thank you we have made some changes to a number of recommendations to reflect the need for longer-term treatments and maintenance treatment.

The issue of publication bias could be addressed better. Specifically, the evidence statements are based on the published literature and therefore represent overestimates of drug/placebo differences. Shouldn’t this be mentioned in the evidence statements and clinical summary sections?

Although we may agree that it is impossible to be sure about RCT data, it can also be misleading to rely on clinician experience. Were not RCTs introduced to get away from reliance on clinician experience - have we come full circle? Why not take patient experience into account as well? Taking into account the experience of clinicians and patients is likely to further distort the data, rather than make it more reliable. This is when clinicians/patients see improvement, they will be likely to attribute it to the last intervention used, with no way of knowing whether it would have occurred without the most recent intervention.

Two components of recovery in placebo conditions are mentioned: spontaneous recovery and the effect of supportive care. This attribution of the placebo effect to supportive care is without empirical foundation. It could also be due to the self-confirming effects of expectancy on experience, classical conditioning, or other psychological mechanisms (see Kirsch, 1997,¹ for a review of data pertaining to these mechanisms). Placebo effects have been found without supportive care. In contrast, conditioning and expectancy effects have been well demonstrated as factors in placebo responding. There are indeed two components of improvement in placebo conditions, and one of them is correctly labeled "spontaneous recovery." The other should be labeled the placebo effect, without the attempt to deal with the tricky issue of the mechanism behind the placebo effect. The placebo effect is the placebo response minus changes due to spontaneous recovery, regression to the mean, etc.

We feel we have given sufficient prominence to our reservations: indeed, other reviewers have criticised us for what we have said!

Unfortunately this is also true! But we have not argued for exclusive reliance on this.

We have 3 patient members of the GDG and have argued that this should indeed be taken into account, and have strengthened our recommendations here.

We are splitting hairs here. We argue that there is an effect of "casemanagement" (CM), and this applies to all treatments. There are also possible "specific" effects on depression, of particular interventions, which go beyond what can be achieved by CM alone. We agree with Professor Kirsch that expectancy is an important component of CM.

Spontaneous recovery is of course itself. contained within CM. There is no substantive disagreement here.

Why is it likely that with greater definition of subgroups that benefit over placebo may well be demonstrable? Isn't it just as unlikely? There is clearly a danger in searching for significance in subgroups when the main analysis in not significant.

No, it isn't just as unlikely. It is altogether possible that AD's work, but that they exert their beneficial effects at a higher symptom level than the ICD10 definition suggests.

Perhaps the most serious problem is the reliance on treatment response (a 50% reduction in symptoms) as a primary measure of outcome. Response rates are misleading, especially when the criterion for response is close to the mean improvement rate (as it generally is) (Kirsch, in press)². The main point is that a seemingly large difference in response rates (e.g., 50% versus 35%) can be entirely due to clinically insignificant differences between drug and placebo responses (e.g., one point the Hamilton depression scale). To quote from Kirsch (in press):

If improvement is normally distributed and the mean difference in improvement is 1 point, then there will be many patients (e.g., 15-20%) for whom the one point advantage will push them into the responder category (i.e. give them a 50% reduction in symptoms instead of a 46% reduction in symptoms), despite the fact that the difference is not clinically significant. For this reason, differences based on percentage of patients responding are misleading, and 15-20% differences should not be labelled clinically significant.

This being the case, the difference between mean change scores (drug versus placebo) remains the most reliable method of assessing the clinical significance of drug effects. At the very least, this problem with response rates ought to be noted in the report.

The other issue is severity. See comment on 7.7.1 - it may be well be misleading to rely on a few studies, mostly with outpatients, that have shown that the difference in response to antidepressants and placebo is greatest in people who have the most severe depression. Studies of people in hospital find smaller differences between antidepressants and placebo than do the outpatient studies.³ Indeed one study of inpatients showed that response to antidepressants was greatest in the least severely ill.⁴ The prognosis for hospital treated depression is also very poor, with studies finding that more than half of adults and an even higher proportion of older people have not recovered several years later.

Evidence of a dose/response relation with tricyclics is mentioned, but no mention is made of the absence of this relation with SSRIs.

Thank you - have amended the section.

The increasing response to drug and placebo over the years could also be due (at least in part) to the coverage of antidepressants in the literature leading people to have greater faith in them (and thereby enhancing the placebo component of treatment). In any case, the hypothesis that it is due to "an increasing tendency for RCTs to be carried out with people with mild disorders" is contradicted by data in the Walsh et al. study (the correlation between initial level of depression and improvement in the placebo condition was .10). This could easily be checked with the data analysed in the NICE report. If the hypothesis is correct, there should be a high negative correlation between year of publication and baseline depression scores.

The Ross et al study is cited as an indication that the placebo response may be short lived. However, there are also contrary data. For example, the study published in JAMA comparing Hypericum, sertraline, and placebo reported zero relapse among placebo responders kept on placebo for an additional 18 weeks after the initial 8 weeks of treatment

The report cites two studies as reporting evidence that the placebo response is greater with mild depression and that the drug-placebo difference is greater with increasing severity. There are also contrary data (see Figure 2 in Kirsch, Scoboria, and Moore,2002)⁵; To quote from that article:

The data presented in the NICE report also contradict the idea that the drug effect is greatest among the most severely depressed patients. Instead, in mean end-point or change scores, it shows some evidence of a nonlinear relation, with the size of drug/placebo differences "unlikely to be of clinical significance" in very severe, as well as moderate depression.

We have cited three references in favour of our position. We are aware, and not claimed, that there is unanimity on this point.

Even this study is not really long enough: you have touched on another major problem in this area -most RCTs are for unrealistically short periods.

One of the references we quoted is calculated on the FDA data set as well. We have amended our text here.

This seems a relatively minor point You are referring to absolute number of symptoms lost- this is a simple "ceiling we are referring to drug-PBO differences.

We disagree: we have given references which support our position.

Some of these statements seem to be supported by little evidence eg. are there really fewer discontinuation symptoms with fluoxetine?, has the use of benzodiazepine to treat agitation at the beginning of antidepressant treatment been supported by trial data?, is it absolutely clear that venlafaxine has more side effects and greater discontinuation symptoms?

If the recommendation about fluoxetine having fewer discontinuation symptoms is from Rosenbaum et al, it is important to emphasise that this study was funded by its manufacturers Eli Lilly.⁶ Surely this evidence at least needs to be replicated before being used as the basis for a recommendation.

NICE hierarchy of evidence states that one RCT is enough for an A level recommendation.

Evidence statements in 8.3.4.14 and 8.3.4.15 have been produced by combining very different trials. Nor do they seem very strong statements, yet 8.3.5.1.4 makes specific recommendations about adding mianserin to SSRIs and mirtazapine to SSRIs, venlafaxine and buproprion. Surely the evidence for these specific recommendations needs to be replicated, or specific analyses need to be shown in the report, rather than using an evidence statement from pooled data. Probably there needs to be more caution about recommending the combination of antidepressants in itself. Why not use the expression of the need for caution, as in the pindolol recommendation?

Thank you. The recommendation has been changed.

It may be misleading to suggest that discontinuation symptoms are usually mild and generally resolve rapidly with reinstatement or within a few days to weeks without reinstatement. A significant number of people do experience discontinuation symptoms of such severity that it seems to make it difficult to stop. Not only abrupt but also gradual withdrawal may be associated with potentially serious adverse effects. Although the pattern may be different from relapse, doctors often misinterpret discontinuation symptoms as relapse, and there may be no defining feature that can differentiate.

Thank you - have modified the text to indicate that symptoms can be serious. Please see chapter 8 where this issue is discussed in more detail.

Is it clear what the nature of antidepressant discontinuation reactions are? How well accepted is the concept of "receptor rebound" in this context? How are discontinuation symptoms related to habituation ie. are discontinuation symptoms a reflection of psychological dependence rather than receptor rebound as such? Is there really enough controlled trial data over a longer period to suggest that onset is usually within 5 days?

The aetiology of antidepressant discontinuation symptoms is not completely clear, there is limited controlled data in this area. We have interpreted the best available evidence on the subject.

There needs to be discussion with patients about the evidence for efficacy of treatments, including medication, and specific discussion of the risks of discontinuation reactions at the time of consent. 2.8.1.2 is not specific enough on these points. There needs to be a more direct link with 8.2.8.6.2 and 8.2.8.6.3

A new GPP has been developed.

There is surprisingly no discussion of whether SSRIs cause behavioural disorders, including suicidal behaviour.

We beleve this has been adequately covered in this section of the full guideline. We have amended the text of the shorter form.

Why C, not GPP?

GPPs are simply recommendations for good practice. C level recommendations are used when there is no direct research evidence (but where it would be possible to design a study to research the matter under consideration) where the GDG has drawn on experience.

Although mentioned elsewhere in the report, a key issue is the rising cost of antidepressants and the need to control pharmaceutical expenditure and company profit.

Thank you this is outside the scope of the guideline.

Is it for over 17s or over 18s? Ambiguity needs to be made clear

Thank you it is 18 years and over.

Misprints - guideline is for depression, not eating disorder

Apologies. Editorial error. This has been amended.