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In the Pipeline
Birth of an Idea


August 16, 2005

Experimental NewsEmail This EntryPrint This Article

I set up another run of experiments in my long-running series today. I'm repeating the best results from last time (the previous post in this category), with fresh samples of everything (just to be sure that there wasn't something odd about the last batch, which seemed to work so well.) There's a new type of control in there, too, off in another direction from the ones I've run before. And I've made several new compounds to test, all closely related to the things that seem to have worked.

That's been a big part of the delay. I've exhausted most of the commercially available starting materials by now - as I narrow down to the most promising structures, I find that I have to make a lot of my starting materials myself. Some of them are easy to whip out, but I still have to purify them, and all these things take time. And, of course, none of this is officially what I'm supposed to be doing, so I have to work these things in as I can.

I've also accepted an offer to present the whole idea in a public forum for the first time. Well, an inside-the-company public forum, that is. I've grabbed folks by their shirt collars and scribbled all over their office whiteboards during the last couple of years, but this will be the first time I've put everything together into a real presentation. My submarine project is beginning to surface.

June 23, 2005

News Flash: I May Not Be a FoolEmail This EntryPrint This Article

I now have my experimental results, at long last. And, well, I have to say that I seem to have something.

This batch was set up with fifteen different chemical structures, and I was looking for the same effect in each run. For each structure, there was an experiment that should have shown the effect I'm after, producing a new product, then a control (without a key ingredient) which should have shown little or nothing, and another control (with the key ingredient present, but with another compound added that should have blocked it from doing anything.)

I thought at first that I had fallen completely on my face, because as I looked over the first five or ten structures, I saw the same discouraging pattern. Next to nothing in the blank control runs, which was fine. But the numbers from the corresponding key-ingredient experiments were identically low, which was the inescapable sign of nothing going on. I'd also seen some where the experimental run showed something, but the corresponding blank showed the same exact levels - again showing that my experimental conditions weren't changing anything, but that I just had a high background rate of reaction.

I was using strong language by the time I got to number twelve, which showed a pretty high value in the experimental run. I looked over to the blank run, expecting to see the same levels, another high-background dud - but it really was a blank this time. Almost nothing there. The experimental run was at least fifty times higher. I held my breath as I looked at the second "inactivating control" run, and there it was -it went right back to the blank value, as it should if my hypothesis was correct. I had set up all the experiments in duplicate, and this morning I got the repeat data, which matched the first set very tightly. It appears to be real.

And to go along with this, these experiments also included the best candidate from my first attempts, the one that got me excited about running these follow-ups in the first place. It had made a lot of product again, although just three or four times the high background rate in the blank reaction, as it had been before. But had the inactivating control experiment knocked it back down to those values anyway? It had.

And both that one and the new winner are structurally quite similar, and they're the only two of that exact class that I've run. It's becoming increasingly clear to me that I finally have something that works, after three years of on-and-off attempts. I hardly know what to do with myself.

Well, that's not quite true. I have another variation ready to go, with ten or fifteen new structures of a different type, and I have time to incorporate what I've learned from this run before they go off. It's time to see just how far this stuff can be pushed.

June 21, 2005

Data, At LastEmail This EntryPrint This Article

A rare mid-day update: finally, after weeks of delays, I'm getting the analytical data run on my most recent set of experiments. These are based on what looked like successful results back in April (see these posts for the details), and if I have any idea of what's going on, they should work.

And that's the scary part. Late this afternoon or tomorrow morning, I'll either know that I'm on the track of something interesting, or I'll have slid most of the way back down the hill. Again. It's been like this every time I've come up to a crucial experiment in this work. As I've said, scientific progress depends, to an unappreciated extent, on the willingness to look like a fool. It's tough work, waiting to find out if you are one or not. . .

June 07, 2005

Experimental UpdateEmail This EntryPrint This Article

Since I mentioned a while back that I was setting up a crucial run of experiments, I thought I should let the (three or four) people who are following this story know what's going on.

What's going on is that I'm slowly chewing a hole through my desk. The instrument that I need to get these samples analyzed went down just as I was finishing up the experimental run. And that's not "down" as in "let's replace the fitting with a new one from the drawer here," that's "down" as in crucial-hardware-back-ordered-from-another-continent. As in two service techs up to their elbows in the thing for three days - that kind of down. As of today, the machine still isn't its old self.

My original run of experiments is probably untrustworthy at this point - I'm saving it to try out backup analysis techniques. I set up another run of fresh ones, which are now in the freezer, waiting to be analyzed when there's something to analyze them with. I console myself with the thought that they must have some pretty good stuff in them, because the universe is sure doing a good job of keeping me from ever finding out.

April 27, 2005

Experimental Update, For Those Who CareEmail This EntryPrint This Article

Well, I got the results of my experiments this afternoon. There might be something there, but I'll have to see the rest of the data in the morning to be a bit more sure. In research, we live for slam-dunk experiments that really prove things, but most of the time we get this could-be might-be stuff.

Most of the reactions did nothing, which was disappointing. Two of them showed what could be a real effect, though, and those two were from the same chemical class. That could be telling me something, or it could be just a coincidence. The analysis of some duplicate runs of the same things will be ready in the morning, and I'll see.

If they repeat, that's probably good news. I'll then simultaneously narrow down and fan out in other directions. That is, I'll set those same reactions up again, and add a few runs that are controlled for against some other variables. On the other hand, if they don't repeat, then I first need to make sure that my wonderful pipetting technique isn't one of the causes, but then I have some other things to try on different systems.

One of the few things I can prove is that not every system I can set up has an equal chance of working - in fact, some of them definitely won't work at all, for reasons that can't be foreseen. Perhaps I've landed on one of these and need to get out into another area - or perhaps I'm just wrong from the start. It's too early, fortunately, to be able to prove that.

UPDATE: Well, all the experiments repeated quite nicely, which is something to be glad of. If I'm wrong, I'm wrong the same way every time. I'm already planning another run of stuff for sometime next week, and I won't inflict the details on everyone until they're finished.

April 25, 2005

Live The Stereotype!Email This EntryPrint This Article

Now I know why all the biologists I know are half-sane at best: it's all that pipetting. I set up my experiment today, in a 96-well plate (here's one similar to what I was using, if you don't know the beasts), and spent a good chunk of the afternoon pipetting in a few microliters of this and a few microliters of that. Over and over. A multichannel gizmo (like this one) would have helped, but only in the beginning. Everything else was special-ordered for each well, so this was going to take some time, no matter what.

Still, I'm glad to have finally fulfilled my research destiny. The biologist-holding-a-pipet shot is third in the pantheon of Cheap Scientific Shorthand images. Just ahead of it is Peering Insightfully Into the Microscope, and at number one (as I've written about before) is Looking at a Raised Erlenmeyer With A Thoughtful Expression.

The experiment will run until Wednesday morning. Then it goes to my colleagues downstairs for analysis, and it's possible that I'll start getting results on Wednesday afternoon. Otherwise, I'll just sit around on Thursday and stare at the phone until it rings. That always works.

April 24, 2005

The Consolations of Pure ResearchEmail This EntryPrint This Article

I mentioned the other day that I'm getting close to another run of experiments on the research idea I've been messing with for a couple of years now. For those who haven't been following this tedious tale, so far I've had - well, I've had no real success at all. I thought at one point that something might have worked, but it didn't repeat in any detail.

So, why am I coming back for more punishment? Several reasons: for one thing, I can now think of possible confounding variables in the earlier runs that could have rendered them unable to work. (Many of these are addressed in the current experiments.) Second, I still - in the face of a fair amount of evidence, I admit - believe that this whole thing should work. Some roughly similar chemistry has worked for others, and I think that my modifications (which should make the final technique much more broadly useful, I think) aren't big enough to mess up the whole system.

And the third reason is that I enjoy this kind of work very much. It's a luxury to be able to work on your own ideas in industry, outside the bounds of a particular project, that is. (When we're working on inhibitors of XYZ kinase, I'm free, naturally, to have any ideas I want to about inhibitors of XYZ kinase.) Doing this kind of blue-sky side work is a nice change.

I'll know in the next couple of days if my colleagues in the analytical group are ready for me, and the first run of experiments will take a couple of days themselves. Then there's the time it takes to analyze them (on the instruments, that is - once I see the data, I'll know in a couple of minutes if things have worked out or not.)

Every time I come back to this work, I have a clearer idea of what's going on, and a better way to see it. If you keep doing that, you eventually break through. Right?

April 03, 2005

Don't Talk To Yourself So MuchEmail This EntryPrint This Article

I've been re-reading Francis Crick's memoir What Mad Pursuit, and this passage struck me:

". . .it is important not to believe too strongly in one's own arguments. This particularly applies to negative arguments, arguments that suggest that a particular approach should certainly not be tried since it is bound to fail. . .While one should certainly try to think which lines are worth pursuing and which are not, it is wise to be very cautious about one's own arguments, especially when the subject is an important one, since then the cost of missing a useful approach is high. . .

Be sensible but don't be too impressed by negative arguments. If at all possible, try it and see what turns up. Theorists almost always dislike this sort of approach."

Right on target. In my field, there is hardly an experiment worth doing that can't be objected to right at the start. Counterexamples abound, theoretical reasons why things won't work out are everywhere. Too sterically hindered, not nucleophilic enough, an interfering functional group somewhere else in the molecule, wrong solvent, wrong catalyst, wrong temperature, wrong everything. If you listen to every one of these objections, even when they're coming from inside your head, you'll never do anything at all. True, you'll never be wrong, but only at the cost of never being right.

This is on my mind tonight, because I'm getting close to a revival of a series of experiments that I've been messing around with for nearly three years now. It's a very interesting idea whose details, painfully, I'm not at liberty to lay out. Not yet. I'm reposting my writings on this work over in the Birth of an Idea category at the right, in case you're interested in seeing what scientific excitement does to a person.

The whole time, I've hardly had the tiniest bit of experimental success, it pains me to say. But I'm back with another variation. Every time I'm more sure that things are going to work. Perhaps, after two years of being quite wrong, I might make the switch to quite right. . .

March 14, 2004

Mismatched SocksEmail This EntryPrint This Article

Some miscellaneous updates tonight, in addition to the note appended to the post below. It seems that Sunday nights don't often leave with time for more extensive blogging, and the world events of the last few days have made their claim on my attention as well. This isn't going to be one of those dull years, not that I expected it to be. In fact, I'm not sure when we're going to have one of those again.

Some readers (rather few) may be wondering what's been up with my long-running series of odd experiments, last seen crashing to earth in a rain of feathers and melting wax. I haven't set anything up in the lab since that, but I've been busy working on a presentation to go public (inside my company, anyway) with my ideas. The project, if it's going to work at all, is too big for me to do in the scientific equivalent of my garage. I'm going to make my case for some formal support, and it'll be interesting to see how that's received.


On another front, I wanted to mention that I closed out my short position in Imclone at about $45/share, a nice round loss from the $40 where I went short. I'm keeping an eye on the stock, and if it continues to rise (up into, say, the 60s with no change in the underlying situation), then I'll consider shorting it again. For now, though, discretion was the better part of a capital-gains loss. I continue to think that many IMCL investors suffer from an excess of optimism, but that's one of the engines of the market, isn't it? (I did make up that loss and more by shorting MSO, Martha Stewart's company, though. Write and I'll bore you with the details.)

And the Sanofi/Aventis dance continues, with Novartis hovering over the whole proceedings. This is yet another situation where those who say, don't know - because those who know aren't saying. Most of the public statements are designed to be, well, merely public statements, so their information value is questionable. It's going to be a while before we know how this one comes out, so I haven't been (and won't be) covering every twist and turn. If anything dramatic happens, I'll weigh in.

January 25, 2004

A Little Ambiguity Would Be Welcome Right About NowEmail This EntryPrint This Article

My experimental results came in late Friday afternoon, and. . .well, rarely have I seen less encouraging data. It wasn't enjoyable. I was there as the numbers for each part of the experiment came through, and I could tell early on that I was in trouble.


So, here's the rundown: the repeat of my previous (putatively successful) experiment failed. Then the attempts to increase the effect failed at each point - if anything, things went down instead of up. Then the attempt to reverse the effect (in four different ways) failed, no doubt because by this time there really wasn't anything to reverse. The best-looking run of the whole afternoon was from this group - but it was, perversely enough, the one that should have been the most shut down. Ungood.


What now? The only way this experiment can be any kind of good news is if some systematic error disabled the whole thing. I would love to find out that one of the components was taken from the wrong vial, or was left on top of a hot plate or something. But that's highly unlikely. But what about that previous experiment, the one that led to this death-or-glory attempt? I'm going to be going back over that one, giving it a fishy glance in light of what happened on Friday. At this point, the hypothesis that best fits the data is that the encouraging results are wrong.


I may still be able to do one more attempt. There are a couple of oddities about this latest data set that I don't understand, and the idea is worth one more shot under the cleanest conditions I can think of. But that, for now, will have to be it. I'm going to have to go back to the drawing board and think about what's going wrong, see if there's some different way to realize what I still think of as a beautiful idea. There may yet be. Plenty of beautiful ideas don't work, though: beauty is necessary, but not sufficient.


Science is fun, it really is. And it's certainly damned useful. But it isn't easy.

January 22, 2004

Dr. Lowe? I Have Your Hypothesis on Line TwoEmail This EntryPrint This Article

I spoke a couple of weeks ago about my latest series of experiments at work, and I've had several inquiries about how things are going. Well, the whole shebang has been in the freezer, actually. The instrument that we need to analyze things (and the person who runs the instrument!) have both been occupied with an unexpectedly lengthy problem in one of our drug discovery programs. My high-risk side project takes a back seat to that, understandably.


But the thaw is coming. I was told yesterday that my samples have moved back to the top of the list, so it's possible that I'll start to get results tomorrow (and if not then, on Monday.) So, here we go. I think that these runs are going to be definitive, one way or another. There's always the possibility of a "maybe" answer when you do an experiment, but the key to successful design is setting things up so you don't get many of those. I think these results won't have too much ambiguity in them - they shouldn't. If they do come back fuzzy, it means that my mental picture of what's going on is faulty, even if my broad idea turns out to be right.


My whole idea is on the chopping block, and the knife is poised to fall. I'm going to be able to look back on this evening, this whole period, as either the last time when I still had doubts about this discovery - or as the last time when I still had hopes that it was real. Oh, science is fun - it really is. And it's certainly damned useful. But it isn't easy.

January 12, 2004

If This Doesn't Work, There's Only Reality To Fall Back OnEmail This EntryPrint This Article

Time for an update on my research, where I'm still working on the odd idea that I've been speaking about. In my last installment, I had what seemed to be good results from an experiment, and I was getting ready to set up some more control runs to see if things would behave as they should.


Well, those reactions are going right now, thanks to the efforts of a colleague in Biology. These experiments will be running all night (Monday EST) and finish off around lunchtime tomorrow. Then I'll take the solutions down to another colleague in our analytical department, and in the next few days, she'll tell me what's happened. The wait will not be an easy one. I can tell that already.


That's because this batch of experiments is actually a pretty strenuous interrogation. I've tried to set it up so that good results can come out of it only if there's something real going on. I think there is, of course, but it's impossible to say for sure. My results from the first experiments could be characterized as "consistent with my hypothesis," but that's all. Mind you, that's a lot better than the alternative, hoo boy, but there could be other (less interesting!) things they're consistent with.


But the reactions taking place tonight should sort things out, but good. This run has four different parts to it: There's a repeat of the most promising conditions from the first experiment, just to ask the most basic question (reproducibility.) A distressing number of interesting experimental results never poke their heads up again, so that's one hurdle. In the second part, there's a set of conditions that should cause a larger effect than I saw the first time. This attempt is being racheted up in two seperate steps. If it goes up nicely each time, I'll be very happy. If the results come back one-up, one-down, I'll be staring out the window a lot, trying to figure that out. And if they show no effect, well. . .


The third part reverses field: it's an attempt to completely abolish the effect, by a mechanism that should be quite specific to my hypothesis. This one's in two steps, too, in another attempt to see a dose-response relationship. Having this one come through, which would revert the system to the same results coming from the corresponding blank experiment, would be strong evidence that I'm on the right track. The reverse holds true, too, unfortunately - if there's no effect here, my hypothesis has taken a torpedo right in its engine room. (That blank experiment is running tonight, too; it's an important control for all these tests.)


And the last ring of this circus is another attempt to make my desired effect disappear. I've changed a chemical structure in a way that should make very little difference to anything, except in the case of my hoped-for mechanism. It should shut that down pretty cleanly. It'll be hard to hold on to my current idea if this doesn't work as planned, either. I'll have to fall back on experimental error, which is not the first explanation you want to reach for, or some other variable that has completely escaped my notice. Neither of those is a good bet at this point; it'd be a lot simpler to assume that nothing interesting is happening at all.


For readers outside the research arena, those try-to-kill-it experiments are a powerful and commonly used technique. It's hard to run them sometimes, because it's hard to escape the mental picture of your new phenomenon, just arrived into the world of physical experience, being scared back into its hole by the sudden advent of search lights and sirens. But, you know, there are a lot of things to work on in this world. And if you don't figure out what's real and what isn't, you can spend most of your scientific career doing the equivalent of digging holes and filling them back in. It's hard on a hypothesis, being put to the test like this, and I'm here to tell you that it's not all that easy on the person behind the idea, either. If something's real, though, it'll show itself - it'll have to show itself - no matter what nasty questions you ask. Better to ask them up front.

December 07, 2003

Good News, Backing Slowly Through the Door?Email This EntryPrint This Article

It's a good time to give a brief update about the experiments that I'm running at work. (The last time I spoke about them was here.) For those who haven't seen one of these posts, I've been chasing an odd idea for months now, on and off. So far, the tests that I've put it to have come up negative - or at least not positive, which is often something different. I've continued to refine my thinking about what's going on while searching for a better system to work with.

The other thing that newcomers to this site need to know is that I can't tell you exactly what this idea is. Now there'ssome great blog material, eh? But I'm hoping that folks will understand. If I were in academia, I wouldn't talk because I would be afraid that someone would scoop me and get priority by publishing first. Since I'm in industry, I worry both about that and the proprietary advantages that this stuff might bring. (If it works out well, there certainly could be some.) Actually, come to think of it, academics think that way too these days, don't they?

I'll try not to be too reminiscent of the South Sea Bubble scam artist that Charles MacKay talks about - the one who advertised partnerships for sale in "An undertaking of great advantage and no man to know what it is." He took in a large sum within a couple of days, and as MacKay tells it, he "was philosopher enough to be content" with his profits, bailed out to France and was never heard from again. At least I'm not selling shares.

On to the news. In my last, er, thrilling installment, I was about to set up (with the help of a colleage over in a pharmacology lab) a new experiment which would be the best shot yet. Well, it took a while to get this one analyzed, during which time the solutions sat patiently in the freezer. I had to remake a standard compound for my colleagues in the analytical group, and they had to work out good methods to run the samples with, which needed something else first, and so on. But we got things together last week, and got the data. And, well. . .the thing might have actually worked.

I was running four separate variations on the same system, and all four did some of what I wanted, apparently. They did it to different degrees, and in a pattern that (if it's real) is quite suggestive. But the whole thing was getting close to the limits of detection - not so close as to make the results totally suspect, fortunately, but everyone involved would be more comfortable with a higher signal/noise ratio.

These results have immediately suggested some follow-up experiments, which I'm going to do with the most promising of those four variations. There are three more components of the system that I'd like to vary. One of them should (helpfully) lead to a stonger signal, which should vary as a function of the component we're adding. That'll be a useful check. And the other two experiments will go the other way and wipe out the effect completely, each by a different route, but only if things are happening by the mechanism I'm postulating. These experiments will carve great swaths through Explanation Space, blanking out whole regions of potential false-positives.

And if these runs go according to predictions, well, I'm going to be in the position of the dog who finally caught a car. Scientists can relate to those dogs, you know. What makes us different from the dogs is, we all know just how we would drive the thing if we caught it, and just where we'd want to go. Woof.

November 28, 2003

Waiting for the Metaphorical Phone to RingEmail This EntryPrint This Article

This week I should be getting the results from a crucial experiment I set up recently. Actually, the experiment is a whole set of them, a good thirty-two of the little things, and the whole lot has been in a freezer for about ten days now. But they're soon to be thawed out and examined.

And I'm of two minds about that. I've written about this before, the feeling that I think many scientists get of almost not wanting to know if something's worked or not. That's partly because the odds are, for any really interesting experiment, that it hasn't worked out the way you wanted.

Now, there are the exploratory sorts of experiments where anything that comes from them is good. But those don't happen very often, generally only when a field is young and there are observations just waiting to be had. In my business, experiments are generally pass/fail grades on hypotheses. And the risk-to-reward ratio that applies everywhere else in the world applies here: the big experiments, the ones that'll make you jump up and down if they work, generally don't work.

So it really is easier, up to a point, if I don't do things like this. It's not like there isn't enough to keep me busy otherwise - in fact, if I want to do any of these no-guts-no-glory experiments, I have to make sure that I don't get sidetracked by the day-to-day stuff. And it's not like there aren't plenty of highs and lows in what we're pleased to call "normal" drug discovery. It should be enough.

But it isn't, not always. These roll-the-dice ideas keep occuring to me, and some of them just seem to have to be tried out. It's hard dealing with the results, which (so far) have been relentlessly negative. That goes for this current idea, which is a little over a year old, and for the ones I've had in past years. None of the really good ones have worked, not one. And that bothers me, as it would bother anyone. But I think, eventually, it would bother me more if I never tried. Here goes, again.

August 03, 2003

Per Fits and Starts, Ad AstraEmail This EntryPrint This Article

Last summer I was working on an interesting chemistry idea. I posted about it on and off, in what was likely an irritating fashion - irritating because I could never quite go into just what the idea was. There were two reasons behind that: for one, my employer gets the rights to chemistry ideas that I work on in my employer's labs, and quite right. (The contracts that you sign when you join any research-based industrial organization are very, very clear on that point.) The second consideration is scientific priority, and scientific pride.

Now, what I'm doing isn't going to win me a Nobel prize, but it is a very nice idea, and one of the better ones I've ever had. So it would be more pleasing to me if I could get it to work with my own hands before letting everyone else take a crack at it. One problem is that I tend to work on things like this in jerky bursts of activity, and those don't come nearly as often as they should. Someone with more discipline would have made more progress, no doubt. A scientist who combined periods of free-association idea generation with stretches of well-structured lab work to follow them up would be the person to have around. I haven't met too many of those people, but they certainly exist. I'm not one of them.

I comfort myself by thinking that the folks with the most disciplined work schedules tend not to have ideas as off-the-rails as this one. It's a common complaint in the drug industry that the work is so ceaseless as to leave people with no time to think. And as I've written before, if you don't have some staring-out-the-window time, you don't have that many ideas. I know that when I've run a project myself, I don't as many good ones. There's no mental overhead left for them; I'm too busy making sure that everything's going the way it should. It's exciting, being at the head of a drug project, but it does wear you out.

Even when you're not running a project, there's always enough work to keep you busy. Keeping busy isn't the problem. The problem is remembering that "busy" doesn't always mean "productive," although they can be mistaken for each other in dim light.

I bring all this up because, as I mentioned a few weeks ago, I'm taking another crack at this stuff. I've been messing around with the idea(s) on and off over the intervening months, but a very good opportunity now presents itself. It's the same core concept that I've worked on before, but (for once) it matches up very well with the project that my lab is officially working on. If I can continue to keep on the tasks at hand, this coming week will see most of the groundwork laid, and the week after that should see the first runs of the real thing.

Here's hoping that I ignore all distractions, and have the nerve to put my favorite ideas on trial. That's the real problem with working on ideas of your own, ideas that you think have the potential to be really good. They don't all work. Most of them don't work. It can be more psychologically comforting to keep them in the "untried but promising" category, rather than find out if they're real.

August 16, 2002

Here It GoesEmail This EntryPrint This Article

The research idea I've been alluding to recently gets a key test today. I've got two values for one of the variables (high and low, essentially) and four values for another. And I've thought up two control experiments for each of those eight cases, which narrows things down quite a bit: under this experimental protocol, good news would have a very good chance of actually being good news.

But bad news would have a pretty good chance of actually being bad news, too. I can think of more ways to see a false-negative than a false-positive, but I'm not sure how likely some of those really are. If nothing happens today, I've got some plans for a second run which would address some of those.

Of course, I'd rather not find myself in the familiar research position of looking out the window, wondering what went wrong. I'll know by later this afternoon. A colleague from another department is setting things up and will collect the data, and I won't be very far from my phone during that time, I can tell you. Waiting for this stuff is nerve-wracking - it feels like I've asked the physical world out on a date and I'm waiting to hear if it'll accept.

Nature Stood Me UpEmail This EntryPrint This Article

. . .not for the first time either, and doubtless not for the last. For anyone stopping by to get an update on my experiment, well, not very much happened. The controls all worked about like I figured they would, but the real experimental cases refused to do anything. And the one run that perhaps moved off the starting point was the one that I least expected to see anything from.

My colleague is going to set up another run in a few days, this one under more forcing conditions (in case I've underestimated the ease that things should occur.) I can come up with a couple of other hypotheses to check as well (as I alluded to this morning.)

But what this means is that (even if my whole concept is right) it isn't going to be easy. It's not like the door is just swinging open to this new field I'm picturing. I'd wondered if it was just because no one had thought to give it a push. I still think the basic idea is sound (although I still have scant evidence for that belief,) but it's an open question how far it can be generalized. If it were as general as I'd hoped, this experiment probably would have worked, frankly.

So, if the door isn't just opening up, the next thing to do is pick the damn lock. I've been uncharacteristically quiet since I got the data today, while I absorbed it and thought about what to do next. But I feel things getting back to normal already. I've got another system to try next week (and I'm working on another new one after that.) And I've had a decent idea to address today's failure, just while sitting here tonight. I'll be back on Monday morning, trying something new. Fortes fortuna juvat.

August 04, 2002

Close to the VestEmail This EntryPrint This Article

Another line in one of the aforementioned Paul Orwin posts rang true for me. He was discussing some new ideas in antibacterial research, then brought himself up short as he got close to his own work: "In the highly competitive world of academic science, even a weblog is no place to divulge current research tidbits"

The same thing goes, with pistachio nuts and a cherry on top, for industrial research. I've hardly said a word about the actual work I do during the day, and I don't plan to, either. It's a pity, since it's been an interesting project with a lot of twists and turns, and it would have been a good illustration of what med-chem research is like day-by-day. But I'd have been fired long ago if I tried to do that, and rightly so. Like all other pharma companies, no one hears a word about what we're up to until we're darn good and ready to tell 'em.

That's what makes information such a strange commodity in the business. The Journal of Medicinal Chemistry("Jay-Med-Chem" to its friends) can be an interesting read, but only in a historical sense. Projects you read about there are either well along in the clinic, or well buried out back with grass growing over them. The same goes for presentations at conferences. When I see a poster from a drug company with a good crowd around it at a meeting, I always think of someone attracting birds by throwing stale bread on the ground.

I've been guilty of crowding around 'em, too, though. I've come back from meetings bursting with the latest news from other companies, as given in their presentations. But we all have to remind ourselves that these breaking headlines are like light from distant stars. Who knows what's happening there now?

This all applies to the research project that I've alluded to over the past few months, of course. It's not directly aimed at a single therapeutic target, but it's an idea of potential usefulness, and my employer has every right to expect me to keep quiet about it. After all, I'm using their facilities to try to make it work. So all I can do is speak in generalities for now, with the hope that if it pans out, that anyone who's interested can read about it in a patent or publication. (Of course, I do have some readers at the company itself, and they've called me up at times to ask me what the heck I'm talking about. I can ease the suspense for them, not that this stuff seems to be keeping anyone up at night besides me.)

This work is on my mind because I'm nearing another crucial set of experiments, as I alluded to on July 24th. All that remains is working out some analytical methods so I can be sure that I know what I'm looking at - and I can tell you, it's a real strain for me not to just go ahead and run the things without doing that first. I could always just put the stuff in the freezer, I mutter to myself, and when I get the analysis worked out, they'd just be there waiting for me.

But that's no way to work. It shouldn't take that much longer to have a well-controlled experiment that I can actually follow. There's another new one coming up right behind that one, and I can hardly wait to get it ready to go, too. Then it'll be time for the "nonspecific elated noises" I promised when I first had this idea (see April 28, also May 2 and May 3 if you're interested.) Or, perhaps it'll be time for some Botox-worthy furrows in my brow, as I try to figure out what went wrong and why. . .

Close To the VestEmail This EntryPrint This Article

Another line in one of the aforementioned Paul Orwin posts rang true for me. He was discussing some new ideas in antibacterial research, then brought himself up short as he got close to his own work: "In the highly competitive world of academic science, even a weblog is no place to divulge current research tidbits"

The same thing goes, with pistachio nuts and a cherry on top, for industrial research. I've hardly said a word about the actual work I do during the day, and I don't plan to, either. It's a pity, since it's been an interesting project with a lot of twists and turns, and it would have been a good illustration of what med-chem research is like day-by-day. But I'd have been fired long ago if I tried to do that, and rightly so. Like all other pharma companies, no one hears a word about what we're up to until we're darn good and ready to tell 'em.

That's what makes information such a strange commodity in the business. The Journal of Medicinal Chemistry("Jay-Med-Chem" to its friends) can be an interesting read, but only in a historical sense. Projects you read about there are either well along in the clinic, or well buried out back with grass growing over them. The same goes for presentations at conferences. When I see a poster from a drug company with a good crowd around it at a meeting, I always think of someone attracting birds by throwing stale bread on the ground.

I've been guilty of crowding around 'em, too, though. I've come back from meetings bursting with the latest news from other companies, as given in their presentations. But we all have to remind ourselves that these breaking headlines are like light from distant stars. Who knows what's happening there now?

This all applies to the research project that I've alluded to over the past few months, of course. It's not directly aimed at a single therapeutic target, but it's an idea of potential usefulness, and my employer has every right to expect me to keep quiet about it. After all, I'm using their facilities to try to make it work. So all I can do is speak in generalities for now, with the hope that if it pans out, that anyone who's interested can read about it in a patent or publication. (Of course, I do have some readers at the company itself, and they've called me up at times to ask me what the heck I'm talking about. I can ease the suspense for them, not that this stuff seems to be keeping anyone up at night besides me.)

This work is on my mind because I'm nearing another crucial set of experiments, as I alluded to on July 24th. All that remains is working out some analytical methods so I can be sure that I know what I'm looking at - and I can tell you, it's a real strain for me not to just go ahead and run the things without doing that first. I could always just put the stuff in the freezer, I mutter to myself, and when I get the analysis worked out, they'd just be there waiting for me.

But that's no way to work. It shouldn't take that much longer to have a well-controlled experiment that I can actually follow. There's another new one coming up right behind that one, and I can hardly wait to get it ready to go, too. Then it'll be time for the "nonspecific elated noises" I promised when I first had this idea (see April 28, also May 2 and May 3 if you're interested.) Or, perhaps it'll be time for some Botox-worthy furrows in my brow, as I try to figure out what went wrong and why. . .

July 24, 2002

Experimental UpdateEmail This EntryPrint This Article

For the six or eight of you who might be wondering, the experiments that I've been talking about on and off for a few months now are back on again. (To catch up newer readers, I've been irritating folks with breathless references to an idea I've had, that I can't detail for proprietary reasons. It ends up like a demented variation of "Charades" where you don't want anyone to guess the answer.)

At any rate, I've found some more test systems that look promising, and that I can get to (chemically speaking) without working up too much of a sweat. These will be exciting to run, because I think they have a fairly good chance of working. And if they don't, that's going to put a dent, a palpable dent, in my hypothesis. Sometime in the next week or so, I'll know. posted by Derek Lowe

May 31, 2002

In Case Anyone's WonderingEmail This EntryPrint This Article

I'm still working on the research idea I've been talking about. New data from some of my colleagues is helping out quite a bit, but it means changing the experimental design quite a bit, too. Beats flying blind, though, I have to say.

Things have moved from the blast-of-inspiration stage to the get-this-thing-to-work stage. That's a longer and slower one, where many ideas die from lack of nourishment. I'm not going to let that happen in this case - if this idea wipes out, it'll be because it just plain doesn't work, not because I didn't get around to properly testing it.

May 12, 2002

Back for MoreEmail This EntryPrint This Article

No earthshattering news from the meeting (not, as you could tell from my last post, that I necessarily expected any.) I did make good use of some of the time, though, by taking a stack of scientific literature with me and (for once) actually reading most of it.

Like most researchers, too often I equate photocopying a paper (or, for the more recent years, printing off a copy of the PDF file) with reading it. This was brought home to me again as I made my way through this stack. The papers I'd taken with me are the ones that come closest to the idea that I've been (obliquely) talking about for the last few weeks. I was going over them hoping to pick up some relevant details that could help out in the next experimental tests.

That I did. I'm now convinced that the experiment I ran last week had almost no chance of actually working, and I'm almost equally convinced that I know why. (I generally find my own arguments pretty convincing, which is a mental habit that can be an equally great strength or handicap. You never really know which until it's too late, though. . .)

At any rate, I think that there's a key variable in my experimental setup that I've wrongly estimated. It'll take a few days to rearrange things to put that hypothesis to the test, but that's the next order of business. Of course, if I get everything lined up and things still don't work, I haven't proven anything. But the changes I'm making make logical sense to me (and to my other co-workers who are helping out or following along.) If things don't work this time, at least I'll feel that I've given them every chance to. And I'll be incorporating these changes in the future variations I've spoken of (the ones that, intrinsically, I think have a better chance of working.)

Whenever you change something in your experimental design, there's always a nagging fear that you're unknowingly about to abandon the only conditions that could make things work properly. In this case, the good part is that the original setup I chose is still available. It's the starting point for the new one, and I can (and will) still take data under those conditions as I go on into the new conditions.

Of course, the downside of testing things out this thoroughly is that your original idea is on the chopping block the whole time. Getting all the variables figured out, thinking through just how you want to run things - these could be just sharpening the blade. The nerve-racking thing about science is that we really do prove things. And sometimes we prove ourselves wrong. . .

May 06, 2002

Meanwhile, Back at the Chocolate FactoryEmail This EntryPrint This Article

The attempt today to put one facet of my latest ideas to the test wasn't too encouraging. I didn't get the effect that I was hoping for, but the data suggest some complications that might have intervened.

The next set of experiments is coming up soon, and I'll incorporate what I've learned this time into their design. Next time I try this particular angle, I'm going to do it with several closely related starting materials, in hopes that some of the factors that complicated today's run might clear up with changes in that aspect of the system. If they do, then it's great news. If they don't, then I can rule out some more explanations of why things are going like they are. An ideal experiment is one whose every possible outcome is full of unequivocal meaning. I can't set up one of those, but I can try to make the ones I have cut in as many simultaneous directions as possible.

I've also received an offer of assistance in the form of another analytical technique, which could prove very useful on its own and as a reality check on the others. If any of this stuff starts to work, I'll need all the reality checks I can get.

May 03, 2002

The Nuts and Bolts of a New IdeaEmail This EntryPrint This Article

Well, Monday will mark the first test of the research ideas that I've been talking about (see the 4/28 and 5/2 posts below.) It's not the perfect experiment that I'd like, partly because it'll be testing one of the less-likely forms of the idea. On the flip side, if this one works, plenty of other stuff probably will, too. I have the starting materials I need ready to go, as well, which comes under the "bird in the hand" principle.

The main uncertainty is still in the control experiments. There's a way that I could get a false positive in this experiment, and there's no way to keep that from happening. It's intrinsic. But there is a way to control for it, leaving out one key factor in a separate experiment. If that run gives me the same result as the "real" one, then I'm in trouble. It'll mean that what looks like a positive result could just be what would happen anyway. I've got several "Plan B"s to go to at that point, other experiments with different starting materials that still might show that the underlying idea could work (just not on the first thing I tried.)

If the results are different in the control versus the real experiment, though, it'll be time to break out the party hats. But I won't know that for a while yet, unfortunately. The complicated part is that I can use a fairly straightforward method to measure how things are going, but it'll only work for the real experiment, not the control. There's a more complex method that'll work for both, so that's what I'll need to do the key head-to-head comparison. It won't be ready for prime time for another week or two; I have some colleagues who are going to work on that for me.

So, Monday's experiment is just a first hurdle. Using the straightforward readout, if the real experiment shows something, that's a necessary (but not sufficient!) piece of evidence. I'll be relieved, but I won't be high-fiving anyone. If it doesn't show anything, though, I'll know to move immediately on to one of those Plan Bs I mentioned.

One of those doesn't deserve that label, actually - it's the system that I think has the best chance of all of them of showing the effect I want. But it requires some chemical synthesis, which is in progress. With any luck, I'll have the necessary compounds made at about the same time my friends in the other hallway get the robust method for comparing the experimental results. When we get that all working at the same time, we'll be ready for some serious moments of truth. Monday's, by comparison, will be a small one. But I'm excited, just the same.

May 02, 2002

Measure Twice, Cut OnceEmail This EntryPrint This Article

Not much time to post at the moment, between home life and work. If this were in my single days, I'd be at the lab until all hours working on the ideas I spoke of, but I don't think my two small children would care for that (and I'm certain that my wife wouldn't!) I give her updates on what's going on, though (we used to work at the same pharmaceutical company, and she knows the field.) Actually, I even give my 3 1/2 year old son updates: "Daddy, did you use your stir plate today?" "Yes, I did!" "Did you use your hydraulic hammer?" "My what?" "Did you use a backhoe today, Daddy?" "Um. . ."

I'm involved now in experiment design, trying to make sure that I control for all the possible explanations of what could happen. I find it useful to imagine myself explaining this stuff to the most sceptical/hostile people I've encountered in my scientific career. Picturing what questions they'd ask is a good way to come up with control experiments to make the results stronger.

It's frustrating not to immediately run and set something up, but a few days spent at this point could mean a lot. An experiment that looks like it might be big, but could also be explained by something uninteresting, is almost worse than having a negative result. With a little care up front, I can avoid that situation completely.