Good evening, everyone. I just like to note here this evening, I'm Jim Olson.
I'm senior counsel in the primary care CDU.
And I, along with me coordinating the clinical statistics, the clinical trials module this week, I'd like to welcome Professor David Ferguson.
Okay. So this is what happens next to each of the officers for about five years.
I still can't remember the name, but I was thinking, I'm afraid I'm not going to see David Ferguson.
If he'd like to give us a really interesting talk about selection bias and cluster randomised trials at deep deny.
First a met in Aberdeen. David then worked as a health economist in the Health Services and Health
Economics Research Unit and then he moved to York A in the Centre for Economics,
and then he moved to be director of the York Clinical Trials Unit.
So he's our method of this now rather than I kept him, if that's what you call himself.
Everybody heaved a sigh of relief about what would be on the methodology and I'd on.
Thanks very much. Okay.
Still said I'm going to talk to you about selection bias that occurs in a significant proportion
of cluster randomised controlled trials and finish with some ways of trying to prevent this.
But before I do, I'll remind you what happens in individual randomised trials and that's why it's been we
know there's been a problem and individual randomised trials for many years that there's a
potential that the randomisation can be subversive and we try and prevent this by ensuring
that randomisation is concealed as third party to avoid this problem of selection bias.
So I'll give you some kind of illustration of why this need try and do such a randomisation came from.
And this is a classic case for kind of Shelton College back in the mid 1990 when I
did a meta analysis and looked at the effect sizes of trials by their allocation,
concealment status. And so you can see that here in adequate randomised trials,
which they did with people not having public access to the allocation in this set of
about 41% increase in effect size compared with the adequate method of randomisation.
And the shown for that time said that an adequate method of randomisation was to use opaque concealed envelopes,
which is still used in about 10 to 20% of randomised control, to still use opaque sealed envelope which are absolutely fine.
If you ever see a trial that uses a sealed envelope to the model of the number or not to trial to uselessly ignore it.
And this is a case that when we were both in Aberdeen for a large randomised
controlled trial that will cost the taxpayer over million pounds in 1990s money,
and that was £1 million of funding worth something.
And we, after about 200 patients were found to be subverted and at the time of five or more centres.
And what happened was that the clinician would approach patients, get their consent to take part in the study,
and they had a box filled number of envelopes and what they were supposed to have had a top envelope and open the envelopes and and within
the envelope would be the allocation of whether that person would get open surgery or lack of access to the statistician at the time.
Well, after about two of the patients was doing some type of training and.
That's right. And for some reason, you compare the two treatment groups and their overall age,
and you can say that the experiment was on average for years and different controls, which obviously shouldn't happen because of randomisation.
And then what he did was he did it by centre.
And you can see if you look at the centre, for example, the average age of experimental patients was 33 years compared to 59 a control group.
Now you don't need to spend five years of medical school to work out.
If you're 33, you're out because there's going to be a [INAUDIBLE] of a lot better than 50, 69.
And so how did they do it? This is one of the centres and the numbers are the numbers were envelope, the envelopes were numbered.
So that person in the fifth envelope should get this patient recruited.
So this should be a perfect correlation between the patient centre number recruited and the envelope sequence.
And in this particular sense you can say to the envelope number 12, there's this perfect correlation.
But after once we get beyond that, what did the envelope?
As you look at that point and button number 26 there, recruiting.
There were papers in the sense that said there are a number that's in advance and then put them the younger patients.
So 75, for example, was put in all men under the age of 40 in the intervention group,
an old men over the age of 40 and the control group and says, I'm completely biased.
A colleague of mine who did a study in this area often hear it.
What she did was took all the Vanderbilt controlled trials published in one year in the main medical journal, the medical journal from jail, etc.,
and clocked them inadequate or adequate and she inadequate concealment of even opaque envelopes 99% of file she classed as being
inadequate all use of fake field envelopes adequate ones with it used a web based or telephone randomisation was difficult,
and she basically found that the p value for those files that envelopes that
2.0 to compare just got over 0.05 for those that will use adequate charts.
So this is the plot of the study. You can see the.
So if you can see the adequate ones, the dark line that can see and this is about 5%, you see about half the trials are statistically significant,
half and not just about what you would expect if you but if you look at the inadequate one six,
the orange you like see more trials that are that are statistically significant compared with the adequately concealed one.
Now, the only reasonable assumption is pattern here for people.
The envelopes have been opened in advance or people are filling the allocation
because I can't think of any reason why people who choose to use sealed,
opaque envelopes to conceal the allocation are able to pick interventions of more likely to succeed than people who use the more secure method.
It doesn't make sense. This is a masterful design.
What she did was took a dozen systematic view of randomised controlled trials that all published in BMJ Jarman and 2012 and said.
And then what she did was extracted the data from the component trials, the systematic review.
So the first one she got the ten papers and then what she did was that she was a matter analysis of age between the two groups,
both with age should be what you should get within a mention of age.
In randomised controlled trial you should get zero heterogeneity because the knowledge we know,
we know the difference between groups is true, which is no age difference through randomisation.
Those should get no heterogeneity and also we should get no difference.
So if you look at the first one, that's the narrative by the IWF there is enormous a 4% to little difference and
I think it's different eight that's less important than the heterogeneity.
In fact if you look at have that for the study that for hideous and it's the only four for trials
showed zero hitches in that rough full meta analysis that have shown selection narrative.
So all those match analysis contain trials but the allocations have been subverted as affecting baseline.
And even if those for one of them the age imbalance at this particular trial that is populated by a host of the trial.
So yeah, that's a very big problem.
So the problem is individually randomised trials is really quite widespread.
It's damaging metal analysis. See, this is a trial where well I don't know about you guys,
but I've read my medical journal with trials and then mainly just to sort of pick it out if taking one to say this is what this was one along.
Yeah, this is a block randomised 54 patient fleet block with seven randomisation centres,
blocks of four cartons of duty, content to cars marked with house officer, all with nurse.
Each card is placed into a envelope and sealed. The block was shuffled and after shuffling the block faces in a box.
So this is a trial with which problem? That way if you don't get it because the statistician on this job didn't observe it either.
The editor of the Journal and the BMJ didn't sit and neither did the statistical editor didn't see it all.
That is blindingly bloody obvious when when you actually block randomisation block for stuff side by side.
So the imbalance can only be half the block size because we've got dodgy business going on.
Southampton V Sheffield how much we can't.
It's impossible and arithmetically impossible for that to happen naturally either.
The lead author who ignored me then I've got to stop fishing on the paper as well on basis of
the lead author sometimes ignores it because I think if some of the statistics are ignored,
if I wrote fascinating, ordinary, well, so on.
So because there might be a reasonable explanation for I couldn't understand what was a reasonable explanation that I got long time ago.
This just happened just as the largest trial in this area.
That lesson I'm a bit of an internal medicine because [INAUDIBLE] have never published anything about attention,
but they should publish this complete twaddle. So what is it?
So we randomised 450 women and over 900 women to undergraduate students to an intervention to try and prevent them.
Would you say they still haven't been sexually assaulted in the first year at university and the intervention clearly appears it worked.
So in the intervention group 5% were raped compared to 10% in the control group.
So halving of the intervention. And then so what's the problem you saw in randomisation was performing 70 blocks of two with the use of online tool
randomisation that was suffocation code to sign for the 52% control group of 60 for the Prevention Resistance Group.
See, the problem then were if you don't, the statistician could fit you in the jail.
They got you've got, what is it three sites block size of two stuff side by side.
The intervention.
You can only be in balance by half block size, which is why they can only possibly gain balance across the whole trial by three participants.
I mean, I've got a level math that surely, you know. That's right.
And that the site found to have half of two is one, three times one, two, three anyway.
So 450 to respond to the control group and 464 to resistance.
So that isn't to me it's what is it, 12.
Anyway, I did write to actually take it back.
You're concerned about half of the students on the publish my lecture about this trial.
And so given that you about that they did a good publisher and the authors responded
by saying that there were 10 to 1 device in error because they had people misspell,
you know. So irritatingly, my name gets me stuff quite a lot.
People from the middle are in the main court with towards the Centre for Progress which donated it.
And so you can imagine if somebody was told to send in the name, somebody would have written it down,
told and someone else would have written that order and then they thought they are two different people and randomise.
And quite a funny that all ten ended up in one group.
I don't know what your probability of of that happen is pretty remote but anyway that passed.
So we know and what is run by for a few portion of the person because they were using small block sizes and and envelope.
And so what about cluster randomisation now.
Cluster randomisation just to remind everybody what the first got to unit the unit of allocation is something like a hospital or GP practice.
It might be stored, it might be brought,
the kind of people in back then you've got the individuals who are associated with that get allocated to the treatment or not.
You have to run lots of stuff to do that.
And then the unit of specimen, the outcome assessment is on the on the usually on the patient, the individual patient at the psychiatric cluster.
And so we've got two elements. We've got potential bias and the actual randomisation to the clusters,
which is the same as that can happen for individually randomised controlled trial then.
But we can sort that out that they look out for.
The next problem of course, which is that tractable is what happens if you have to recruit the participants after you randomise.
So. Selection bias can be randomised to clusters so long as you've done that properly by an independent person.
You've got balance about the quality of that. What were all happened to that then?
What really happened? How the selection occurs is when they start recruiting the patients actually randomise because
just as individual randomisation is typically because people know the allocation in advance.
So it's just that because you have two people who know the allocation back to the clinician,
those allocation who can then select patients to go in for some reason or, or you can have the patient and the patient that is the across allocation.
So they can volunteer to go in the study directly between the physician.
So you get clustered. But the first time I sort of tweaked this was back in the nineties when I first met some
of these people with the health problems on a lot of back been beans and we would have
done a pilot very complicated design to my ex boss for my being had followed me around
New York so I was working with him again and so he loved having very complicated design.
And this was that the initial design for this trial was a cluster randomised flip flop design.
And so we did a pilot before we launched the main project check the cockpit design work.
So we ran the so to show you what happened at those 26 practices with some kind of
stratification to randomisation bums on the number of the patients in the intervention group.
Then you see training that was management so that GP's and practice managers would receive some training on how to manage patients with low back pain.
Basically try and get them to be mobilised as much as possible because lying in bed, much more chronic, like with make it chronic to train those.
And it's almost obvious in hindsight what would happen if you're telling me about back pain.
I didn't find patients back and hey presto, that's what they do.
They identify a lot more patients, the usual category for that problem than usual practice.
So by recruiting more than 2 to 3 times more patients than the control group.
And then when you look at the baseline values like Rutland Life Disability School,
Aberdeen Back Pain Scout and FFO six can see, quote, higher scores of those two is worth and the low score is worth that.
So you can see the outcome. The main outcome would be the vote in my score.
So the patient team, before they have a chance to get any kind of advice and treatment that the fact this was a significant work.
So we have to abandon that trial because it was it was helpful.
So fortunately, we've done a pilot, so we just then moved on without the cluster element to the study.
This is the recruitment graph that we saw for the intervention for flu and we can see the old way through was like a double number of recruitment.
The good the only good thing about this pilot study is it shows that if you teach,
if you train GP's about a clinical condition, they will recruit more for you.
So if you want to do it, you do it in a randomised trial in primary care we want to enhance recruitment training and they will recruit a lot more.
So I wrote a paper about partly about this and suggesting that we should avoid cluster randomisation at all costs.
And so what I recommend is that is that we should try and do individual randomisation for possible and out of
these if you've got some contamination and I feel hold ups and if you've got contamination that goes up to 30%,
it's still more cost cost effective to do the individual randomisation cluster.
Okay.
So in 2002, I inherited the trials in York and one of the trials had been done at that time, remember too from before for the cluster run Photoshop.
And what we want to work is shoulder pain and they we're going to recruit patients who showed randomised
the general practice trained GP's and then recruit the patients as a group of patients shoulder pain.
And then we would look at the outcome of training on the GP,
on the patients outcomes to see if it got better off patients, GP to being trained to deal with.
Shoulder problem. And so when I joined it, I said, we really need to change the design,
that the design and in the first place, we need to change the design here because it will be catastrophic.
So when I go and if it were so chopped off the place up there, Japan obviously would have to contend with the several of them.
And I couldn't persuade anybody else that we needed to change tack here.
So we had a first draft committee, steering group steering committee statement of the owners.
And so at this point, we could see. We have doubled in the chain saying GP so we could double the numbers of patients.
So at this point I said, look, I know you thought a lot is wrong.
I don't know. I think psychology helps with that because I think you shouldn't have it.
If somebody is doing something, it's catastrophic and you've warned them against it.
And I think it is probably problematic to tell them, I've told you so.
You're supposed to set you know, you're not supposed to cry over the.
But I think I can do that. I've heard that.
Yes, you've got it wrong. We don't know. I may have had an external still.
Have a quick look. The person from the audience they're not have external statistician that who said
we clinch an argument with that difference isn't statistically significant.
My account for that was I told the story of the jumbo jet that flew over Indonesia in mid seventies when
the volcano was going off and it flew it flew through the volcanic ash and all four engines will come out.
So this is the analogy that you're positing said aeroplane 50,000 feet,
all the engines have shut down and the co-pilot comes on and says, we've had a little trouble.
All our engines have lost power, but don't worry, we've lost a thousand people.
That's not an awfully significant. My view, if I was a passenger, is in about half an hour, an hour, it's going to become bloody.
I have no idea that somebody has won it. At least one of the engines restarted.
Fortunately, they got three of them off in one state.
But I would say that it's not that it may not be statistically significant, but it's going to be if we carry on and we catch up not to the authentic.
I told you so then I didn't tell you that at this point it was too late.
Now we are discussing.
So of course that's what's going on.
We need more evidence. You go on about you think that is probably a one off.
So a group was got to try and prove that this is a major problem.
So we did a systematic review of well first published in the BMJ last year in the Journal, met us for five years from January 7th, October 2002.
And so what you find we found that on the first cluster trial,
about 40% was showing evidence of selection bias would tell by imbalances in their recruitment values or in covariate imbalances,
all based on covaxin policy. And in fact,
that's an underestimate because we came across another trial that published a secondary paper after they published a paper in
The Lancet after was published that demonstrated data and admitted they had a selection bias of 40% actually in the letter.
But you know, both those data a long, long time ago, so they do things differently depending on who said this happened.
Unfortunately not so again, when doctors flipped the switch published in 2008, another that and where are we.
Yes about 35 for trial that then showed recruitment bias is possible at five.
Does they have clear evidence in that in the paper that there was recruitment by more than
a thousand to the more recent cluster trials and she found huge problems of the 23 trial.
She looked at about 48% of a high risk of selection bias.
Now, something else she did was what I showed you before an individual randomised trial.
She did looked at the heterogeneity again.
She extracted all the baseline age of all of the 23 cluster trial and then looked to see if the baseline imbalances and what heterogeneity was said.
We have one, two, three, four, five, six,
seven plus the graph where the statistically significant imbalance in eight and look at
hatch American not 3% now remember these are corrected to remember we're looking at.
Limber up the knowledge to hear.
This should be no different. They should all be. The differences make an individual trial that physically fit.
And may even be statistically significant in my chance. You wouldn't expect this.
As I said, this is what you should be fed.
This is the individuals and the lifestyle that are not even myself taking the stage at them for the same issues.
So to put it ten time, this is what we've got to do a better analysis of individual randomised trials.
This is what you expect to say i squared 0%.
We have a tiny, tiny difference which is nowhere near.
We have two trials that have significant imbalances.
No one goes a long way, really goes with what? Which is about what to expect.
So this is what this is the difference.
We would hope to see if we'd done the task, but we're not doing this trial with individually randomised trial yet and we have an appalling situation.
I'll go through a quote, another case study. This is published a couple of years ago and got a lot of it, got a lot of press attention.
I was able to use scientific contact information for Common Output published
and I gave the new scientist a journalist saying how awful it was to publish.
Unfortunately, she published.
She gave a synopsis of the trial and said there was some controversy about it, but the conference is just me ranting to an hour ago.
So this is I mean, this is to stop trying to stop teenage girls getting pregnant.
So the of the randomised schools to have identified about 50 and they get randomised to get a baby simulator.
So the girl has the weekend with a baby that cries at regular intervals, keeps up all night, nothing changed and fed all the cows.
How anybody would have a baby knows exactly what it sounds like.
And so the heart of all of this is supposed to put the the the mothers are the potential as it's the young women of getting himself pregnant.
Now what is so statistically significant, different half of like 1.5,
but it actually shows that the risk of getting pregnant in the intervention doubled the risk of the control of the birth.
Then what we got had a baby compared to 4% control group and they did all lots of fancy statistics, very healthy babies, about half the p value.
But the difference is, I don't know what a block binomial model is for anyway.
We do that for all that us or looking at high quality data.
But do we believe it? Don't believe a word of it.
It's just, you know, statistics are meaningless if you've got awful data looking over data.
This is selection bias on a massive scale. What the NHS thinks, and I think it was a baby doll simulation might actually increase pregnancy rates.
They've gone to NHS choices.
You'll find that this sort of study design with some sort of statisticians, the audience won't go to that paper, do some calculation.
We've got that wrong, actually, but that's a minor problem. We've got the sample. So I've talked to a lot of it.
I tend to look at sample size calculations very easy as why I do, but I'm not going to pay attention quickly.
Do them. Because if the sample size, if you can't get sample size calculations wrong, which is right,
which is a piece of cake, you can do it and you have to write just about a tiny bit.
But then if they don't get that right, you know, then we get anything else like that.
Okay. But this is a good study design on a sample size.
So there we have it. Thank you. So I went to I decided to look for higher soul and more thought of some sort of evidence base.
And so I naturally take that email for the Daily Mail Lifelike Baby Doll designed in 30 days, just from having children actually very pregnant today,
quite intensive search of size, attention to details when they were looking after the dolls, encourage them to have a baby.
No, it doesn't cause a trial to say anything of the kind.
But is it true? Well,
it must be true because NHS choices on the Daily Mail scientists and they both say
that giving infants simulated teenage girls increased their risk of pregnancy.
I like to I have no shares in infant simulators.
I think that probably don't work. But I certainly this shows that I don't have shares in that and I don't care one way or another about them except.
Well, I mean, I suppose in some way I'll stop wasting money on them.
We think let's have a look at well, I won't get into the sample size so that you do that yourself.
This is what. So that's a bit of console time. So they want to buy 57 pills, put it on control to protect themselves.
Right now, first thing we look at is the eligible students, because the proportion of the population in all these girls,
3150 girls compared to have one of them girls that is you balanced population.
If you if you include all those girls and intention st analysis you get them but estimate the truth
so they didn't do that there's enough to go to you want to take part but only half equivalent.
So even if they even if you've got the same something proportion in both total imagine doing it now imagine trying to publish an individual
randomised control trust where 50% of your of your randomised samples are locked out and then you have 58% in the in the intervention group.
But we have an 8% difference of quite a large difference in the number of girls in two groups.
So this eight that immediately introduces selection but over and above any selection bias and then observable characteristics both.
Based on that, you probably taught an office so I teach my students don't have a baseline character
that baseline comparison to the main test what's the argument but there's not that.
Well, we know the knowledge. So if you get the gist, the significant difference difference.
So I'm changing my mind on the type of work and I feel like, oh, all the time about how we should pivot.
The pattern based on variables are not the reason most people do it.
Fact randomisation is work to look for selection, but I'm slowly gravitating to that.
This is in The Lancet. So we've got our P values, but I've got my friendly statistician to my let's have a look.
But this is trying to look at what type of main students what the numbers proportion of difference is huge the p values of scale.
If we look at this now the these are teenage girls getting pregnant so we can expect socio
demographic characteristics to be a high predictor of chances of getting pregnant as a teenager.
And if we look at the factors, demographic P values, got it while we look at it.
So we look at the lowest proportion of socioeconomic factors.
We have 13 5%.
So that in the intervention group, 13% of the girls are from the lowest 10% of socioeconomic status,
compared with only 5% of the of the control group that we look at 17 now an alpha somebody and so you might
do a propensity score matching you might or whatever stuff to try and control for observable imbalances.
But I can bet there's a caveat in that that is not measured,
but not that you are not controlling for in your analysis that gets rid of this horrendous bias.
So because of the crude but we are missing 66 missing we're missing ten in 66 girls in the control group.
And these are predominantly from from socioeconomic group.
So that's a higher rate of pregnancies.
So if the pregnancy rate was 50% or greater among these missing girls, then there's no difference between the two groups.
Now it's 50% pregnancy, very likely. I did try and look for pregnancy rate of girls in Western Australia.
Teenage girls as far as I can find on the internet. There's no routine data published between date.
I don't know what you need to get my social status.
However, I was work on a trial for the AMP trial where we were randomising pregnant teenagers to go to get support from getting pregnant again.
And the pregnancy rate among that group was 66%. So it can be really quite high in some socioeconomic, but not unlikely.
So this is the first calculation of this, so that we can target three one,
3001 and 50 eligible 2100 eligible and simulate a group a difference of 8.45%.
So we're missing 266 girls because we both applied with the total intention to take three population, figure out 158.45% to get 266.
And then we can work out if calculation,
we can then work out the likelihood of what the pregnancy that would have to be to make sure that does not affect all of the simulated interesting.
If you go to that when they did this calculation, which is wrong, nothing's wrong.
We can look at that one figure.
The quote is that the. They expect that to be a 16.8% pregnancy rate.
And this cohort of girls, that's what the historical data says.
On average, 64 ex-employees gave that pregnant. That's what they use in some sort of calculation.
Now the pregnancy rate in the.
Intervention group. And up was 16.6%.
Yeah, 60 left in the control group was 16.6%.
The intervention group was was 15.6%.
So for the infantry group was 16.6%. So the intervention group, which had the highest compliance rate,
had a pregnancy rate that was equal to the historical pregnancy rate average, virtually identical.
The intervention group had a lower pregnancy rate. So why would they why would the intervention so much lower?
It's because of selection bias. So.
To symbolise the claustrophobia. A huge proportion, just a child.
Since I've been working with that, it's terrible. 20 years ago.
That's still terrible. You still can you still get that baby simulator.
So if you try, you try to publish a random individual Monsanto trying to into that reject my letter pointing out the problem with this trial.
I've got no athleticism but in that at least the New England Journal of that so they are but it seems to be I don't know why journals
publish well high profile journals publish I mean should publish this child should publish as a letter of warning to history.
This is yet another fact we designed to stop, but we don't publish it, that we can actually take any meaning from them.
So what should you do about it?
We should try and do individual randomised to go farther for possible and a lot of people do trust the trial to avoid contamination.
So when I was sitting on a one of the study board,
the stated it was the trial which I did my best to stop because they wanted to do cluster randomisation to try and reduce contamination.
So yeah. So after reducing this pattern thinking patients might talk to each other.
Well, I don't know about you when I go to my GP. If I go to my GP because I'm ill, I get the GP but I'm waiting for five of of sick people.
The last thing I do is talk to not because I'm particularly uncertain which I am,
but because I've got the lurking and I don't want to come out with what I've got and what they've got as well as I sit well away from them.
So I talk to the best patients.
They wanted to do just that.
I said, Well, anybody who's had any had a child knows the the social group of young mothers is not wanting from their GP practice.
It tends to be women better than 50 classes. Or that's the group that my wife had as a sort of group that came from lots of different GP practices.
That contamination is an overrated reason for using cluster randomisation.
So here's an example of what they wanted to do, but that is some kind of public health intervention from 1970,
and they wanted the heart to run twice 2000 participants instead of 1282 because of clustering.
So another way of looking at the randomised 2000 people,
one than an individual randomised trial and said what could we have detected so that we could have detected a 7% reduction in smoking.
Right. So let's assume that is a 9% reduction in smoking,
but we actually saw a seventh reduction that because 20% of the sample contaminated and that's assumes
the contamination is as effective as being delivered by the health promotion field the same time.
So that's not likely to happen in particular set of the cup point.
So if you get if you are pretty sure if you get contamination above 30%, then you can trust the randomisation to avoid the contamination effect.
So is it possible when we looked at this 24th draft,
only the third individual randomised trial and the responses to this technique will also comply, which causes best case analysis?
What's the instrumental variable? Technically,
using the RANDOMISATION instrument that can give you a high estimate that if not an unbiased dilution effect of the mass contamination and again,
it has the same powers and I treat it as a as an ordinary analysis if the contamination is central.
So if you still want to go out first and three randomised before randomisation so that you could use it to address the trial on that.
So what you would do is you would approach the schools or 57 schools before you randomise them just as you would do it, an individual randomisation.
You would contact the girls and their parents to get consent to go in trial.
Then once you've got consent, they will 3000 odd thousand and 5000 or so altogether, you might say, okay, 3000 of them in that test.
Once you've got the consent in the bag, you've then randomised the schools and those girls consented in the intervention.
Schools are invited to participate in banged on about the here and the UK being which would have done that.
What we could have done is identify all people with back pain in the fifth vote and ask them if they
would want to take part study where we observe that the severity of their back pain over time and yeah,
chunk of them would have said yes once we've got them in, we would have them at the bypass and then followed them up the shoulder.
Pain trial. We couldn't have done that because it was an incident condition, so you couldn't so you can do it with prevalent conditions.
So the pregnancy stage is a condition that's going to happen.
So you can recruit the girls a long time before the event occurs.
But if you've got five shoulder pain, you need a treating there and then you can't do prevalent recruitment.
So the two approaches could deal with it. First, you can try to match the person doing the recruiting.
So a trial of mental health intervention to try and improve the care of patients with depression and train the GP receptionist to attend,
to speak patients,
to come in and to identify those that may be suffering from depression and then ask them to go to trial before they from that same the same technique.
So the hope was by not by using a receptionist to do that, it would alleviate the.
But then they couldn't do enough to show off and showed us the trial time.
We could we could have done that. What actually cast aspersions on the people during the show came from some ways because what they did,
they originally proposed to MRC this cunning design as a split prop design because basically you randomised
to a group interventions to check whether treatment by changing GP is is better than an infection.
But we can't compare that because these guys, as we can see on that recruitment graph,
these guys are recruiting different sets of patients more to perform a certain equipment set.
So what we do is a patient pitches of cells and at this point they're then randomised to see their
GP or randomise to go and see the mythologies because the rheumatologists are doing the training.
So you would expect if the GP you want to get the GP capability dealing with this problem centrefold and the control group,
you do the same thing and get you involved in talking to right now if the GP care is the same because we've been told it's an intervention group,
these guys that the outcomes are the same.
And also the fact in that group is another effect which is that the GP is as good as the rheumatologist anyway.
Both rheumatologists and trainees not adding anything on to his effort is is equal to still equal.
But but what you'd expect of the intervention was was better in the GP care would be better.
That is a positive result that the GP thought during the training were.
Okay. So when is it not a problem?
So it's not a problem if you if you say the allocation is a lot, if you alter behaviour.
So for example in the U.S. they did under my hospital a year, two different countries pay different, different hours of work.
So junior doctors were on what you do on long hours or the hours were curtailed and the intervention groups that worked on that 40,
50 hours a week and the outcome with mortality in the hospital.
And so in that case, patients would be sent to hospitals.
The patients don't know the hospital visits. It's unlikely patients who get referred know it by whoever is the first hospital,
by the knowledge, even if they knew that the doctors are being paid that way.
But that's in light of the fact.
Similarly, if you run out of randomised compulsive flu vaccinations to try and reduce flu related mortality among their patients,
again, patients are unlikely to know that happening and patients are unlikely to be admitted to not be in this hospital.
On the knowledge that that there's a trial for that and likely selection bias, this is possible and very enlightening so.
So to sum up so that the boss said this is a huge problem, individual and box office continues to be a problem.
I think the problem, worse and worse, the staff and general staff seem to do it.
I think I look back and I remember the last people who got them off in order to get out of the money that comes along in the work and
plus the staff and was run by politicians and all they had to do was grinding on about how to deal with people cluster level techniques,
frailty, analysis, and all the stuff that normal people like me don't understand.
I think it doesn't matter, you know, if not, if you still doing a biased cluster chart, does it matter which technique you used to do the analysis?
It isn't an answer that anywhere near the truth you catch up to question.