Tuesday, September 29, 2015

Stacking the deck with images?

I wish that I could solicit input on this question as an unbiased observer. Anyone who's read my previous posts knows that I am anything but. I considered presenting this data absent the source, but anyone with 1% of Sherlock Holmes' sleuthing ability would track down the paper I am referring to in a nanosecond.  Going back and forth with the EIC at ACS Applied Materials and Interfaces recently (maybe more on this later) forced me to look at aspects of this paper in greater detail than I would have otherwise. As I documented before, one of the reviewers fixated on the cell imaging aspects as a defense of the results, and a rationale to reject my Comment. In preparing an appeal, I looked more carefully at the cell images

Here are cells treated with Fe3+ and probe:

The difference between a) and b) is 1 hr of incubation time. Ref: ACS Appl. Mater. Interfaces20146, 18408–18412

Here is the control of cells treated only with probe:
The difference between d) and e) is 1 hr of incubation time. Ref: ACS Appl. Mater. Interfaces20146, 18408–18412

Notice any differences? I am not very experience with growing cells, but to me it looks like the confluency is much higher and the cell size is larger in the images of the iron-treated cells (Figure a-c), than the sensor-only cells (Figure d-f). This could create the illusion of a greater fluorescence response in the iron-treated cells. There is simply more sensor present per unit area, and there is clearly basal fluorescence. In fact, I might argue that the sensor-only cells (f) are not even healthy compared to the Fe3+-treated cells (c). It also appears that the fluorescence images of the sensor-only cells are out of focus. Even the brighter cells in the middle of the field look fuzzy. Again, this could make the response look more dramatic than the reality. There are other problems with this experiment related to metal transport, but I don't want to conflate imaging with biology. I have a biological interpretation backed by literature for what they observe in the Fe3+-treated cells.

I am interested if anyone concurs, or if I am the victim of confirmation bias. There have been several notorious examples of image manipulation including cut & paste to make nanochopsticks and reusing old data. This isn't that kind of malfeasance, but could it be stacking the deck to fit a preconceived model? How say you?

Friday, September 11, 2015

Fe(III) sensor saga continues

A few months back, I blogged about a paper on iron sensing by Belfield in ACS Applied Materials & Interfaces, and my efforts to bring my concerns about the validity of the conclusions to the attention of the editor. While those efforts were failing to get traction, I brought up similar concerns about a paper in EurJIC. The editor at EurJIC requested that I write a peer-reviewed "Correspondance" on the issues after the author was unable to satisfactorily respond to the criticisms in private emails. Having started the correspondence process with EurJIC, I realized this was also the only recourse I had left at ACS-AMI. A similar mechanism was mentioned in passing by the EIC of ACS-AMI as the only option once a paper was published in the journal, so I decided to submit a "Comment" to ACS-AMI

Obviously, since both papers deal with Fe(III) probes, there are some similarities in the problems as in many other published reports. There are some notable differences as well. In short, the EurJIC paper utilizes PBS buffer and reports a fluorescence quenching mechanism. I indicated evidence of particulate iron and speculated about alternate explanations for the fluorescence changes. The ACS-AMI paper reports fluorescence enhancement in unbuffered water, which I concluded is a clear indication of protonation instead of Fe(III) binding. I very confident in my critique of the ACS-AMI paper because this is exactly the same problem that my group investigated previously with another (very similar) probe. I received a rejection of the comment Friday. Two positive reviews, both suggesting minor revisions, and one rejection. 

Although anonymous, I have suspicions that the rejection was written by an author of the original paper. I conclude this because 1) the authors should have an opportunity to respond in such a situation, and 2) the phrasing of the arguments. I wish that I was surprised that the EIC decided to side with the single "Do not publish" referee and didn't leave an opening for appeal. From the beginning I surmised that the EIC had little interest in criticism of the paper. As a reminder, the lead author of the paper in question is a member of the ACS-AMI editorial advisory board. The dissenting referee made some flimsy arguments against Fe(III) hydrolysis, and focused on the "validity" of the cell imaging studies as a reason to reject the Comment. I specifically did not address cell imaging because sources of false positives in imaging studies are elusive, and more often unrecognized. In the Cu(I)-sensing field, as well as sensing for other metal ions, colloidal aggregates are just recently being recognized as a significant (if not primary) reason why many probes respond  in cells. This is one possible explanation for the imaging results using the Belfield probe, but it is equally likely there is an unknown mechanism that can produce false positive in Fe(III) systems.

The EIC further cited non-disclosure of the Correspondence at EurJIC as an additional rationalization for rejection. This appears to be a thinly veiled insinuation that I behaved unethically. To be clear, no attempt was made to conceal the existence of the Correspondence. I didn't cite the unpublished Correspondence in the Comment due to the lack of a journal citation at the time of submission, as well as the differences in the two systems. I went to great lengths to perform a non-repetitive analysis, even though the underlying issues of Fe(III) hydrolysis are identical (e.g. I needed to cite the same pKa values for hydrated Fe(III) in both articles and it's difficult to express this uniquely). Owing to the different types of experiments performed in each case, I believe that the Comment highlighted a different set of problems that lead to incorrect conclusions. I am not impartial in this case, but I believe people can still write on the same topic more than once in the scientific literature. Many authors, myself included, have been asked to write reviews on the same subject for different journals and therefore reach different audiences. After receiving referee reports from ACS-AMI, I can certainly imagine having revised the Comment with a citation to the EurJIC Correspondence with some additional discussion to address the referee suggestions, although I feel it would confuse the situation to make a close comparison of 2 systems that exhibit different signal transduction pathways.

Furthermore, the EIC suggested that my group should "[carry] out its own investigation on these sensor systems". If one looks at the synthesis of the Belfield probe, you quickly see that this would be an significant commitment of time. The probe requires a 6-step synthesis with a late stage macrocyclization step that proceeds in a reported 20% yield. The only positive outcome of such an effort would be disproving a published paper. A truly comprehensive investigation would require re-synthesizing and re-analyzing dozens of reported Fe(III) probes. This is not usually the kind of study that the community is excited about publishing. This is definitely not deemed fundable research by granting agencies. My aforementioned Inorg. Chem. paper that included a re-investigation of an existing Fe(III) probe as only a small component of a larger study was deemed unimportant by one referee for exactly this reason. Fortunately, that paper was handled by a diligent, thoughtful editor and was published anyway. Again, I am not impartial, but I feel the alternative resolution was proposed by the EIC at least in part because no rationale PI will undertake such an investigation in the current publishing/funding climate. So where does that leave the ACS-AMI situation? I am seeking the input of my scientific friends and colleagues. I have considered the following options:

1. Do nothing. Let this decision stand and move on to bigger and better things. Certainly the most rational course of action from one perspective. The problem with this choice is that the ACS-AMI paper has been cited by authors on multiple occasions as a defense when I critique their experimental protocols/data interpretation in manuscript reviews. This has happened several times in just the last 3 months. This is how these erroneous ideas have been perpetuated in the literature, and it will only get worse.

2. Conduct a study. In the Cu(I) field, it has been proposed that any imaging study should include a control where cells are treated with a structurally similar probe without metal binding ligands. In the case of the Belfield probe, this probably would be some dialkylanilino-BODIPY derivative. That's a pretty easy easy compound to make, but does not create a complete story without the Belfield probe for side-by-side comparison. This returns to the problem of time and resources. Also, what journal publishes such an investigation? It is highly repetitive to say that I am not impartial, but recent history suggest that ACS-AMI won't be particularly interested in this study.

3. A wikileaks-like information dump. No matter what direction I choose, I feel that it would be justified to "self-publish" the Comment here (although the information is already covered in the blog) as well as the referee reports and EIC feedback from ACS-AMI. I have nothing to hide, but what are the ramifications of such an action? Even with full disclosure, I can't escape the feeling that this is such a niche area that the impact will be minimal unlike more prominent issues that have captured the attention of chemists.

What do you think? I'd love to hear your comments and suggestions.

Friday, March 27, 2015

Tilting at Ferric Windmills

As documented last week, I contacted a journal about very questionable methods used to conclude ferric iron could be detected by fluorescence methods in water. I was already aware that this was not the only occurrence of a research group failing to properly account for the aqueous solution chemistry of Fe3+ in their studies. With a reignited hyperawareness about this problem in the fluorescence sensing field, I noticed another study making similar mistakes while catching up on recent literature this week. I alerted the EIC of this journal to the problem as well, and got a completely different response with respect to both the scientific and peer review concerns. Since this is an ongoing dialogue, I will not comment any further until the issue is resolved. This second incident prompted me to conduct a more thorough investigation of the underlying prevalence of these protocols in Fe3+ sensing.

Counts of papers containing questionable ferric sensing methodologies.
*indexed in webofknowledge as of 3/26/205.
Using webofknowledge, I searched the combination of (ferric OR Fe(III) OR Fe3+) AND (sensor OR probe) AND (water OR aqueous OR buffer) AND fluorescence. To decrease the volume of references to analyze, I limited the results to those from journals published by the ACS, the RSC and Wiley since they have a reputation for publishing reliable sensor papers (reducing the number of results from ~500 to ~150). I then went through the search results looking for evidence that the experiments would be at risk for giving spurious results. I am not sure about the exact speciation/stability of Fe3+ in mixed organic/aqueous solvents; however, my experience suggests that any significant amount of water will be problematic. I excluded several studies using 1% aqueous content in solvents like THF and methanol, as that seemed to be a relatively safe protocol. Anything with 20% or more water made the "suspicious list". The overwhelming majority claimed to work in pure water, aqueous pH ~ 7 buffer or with 50% or less organic solvent added to water/buffer. There are many fewer (not counted) that describe protocols for working and handling Fe3+ in acidified aqueous solution, and many others using pure organic solvent (also excluded from consideration). Of the 150 results, 51 contained possible problems. The results broken down by publication year and journal name are shown in the figure above.

The results are quite informative. Before the Rurack paper in 2005, there were no Fe3+ sensing papers in ACS/RSC/Wiley family of journals using water (his paper has been cited >250 times). My paper showing the errors in Rurack's aqueous results was published in 2010. The yearly trends however, suggest that the acceptance of questionable (invalid) Fe3+ titration protocols are increasing rather than decreasing. Presumably, every published paper using similar methods provides unwarranted precedence for adoption in future studies. Whether there is a connection or not is unclear, but Inorg. Chem. where my paper was published, has not published a problematic paper in the Fe3+ sensing field that I can find.

Full disclosure, there are a few papers in this collection that are difficult to analyze, particularly those from the polymer/materials literature. A more thorough investigation would be required to fully evaluate the results in detail. Furthermore, some of the studies have ambiguous or nonexistent experimental protocols in the paper and/or the supporting information, which makes evaluation difficult or impossible. If procedures for measuring/adjusting the pH are not listed, I assume that this was not a consideration. A few papers don't even list the counter ion for the Fe3+. Also, I excluded papers that may have had questionable handling of Fe3+ solutions (selectivity studies), but the Fe3+ response was not a significant component of the paper's discussion/conclusions. The 51 papers all attempt to conclude something specific about Fe3+ detection in aqueous solution. No papers from Elsevier or Springer were examined.

There are some common issues in many of the 51 papers. For example, making stock solutions of FeCl3 in water by just mixing (i.e. without adjusting the pH to <4), and titrating Fe3+ into neutral aqueous solution. Some use phosphate buffer, which would generate Fe(PO4), a water insoluble salt (assuming all the Fe3+ wasn't already precipitated as insoluble Fe(OH)3). A cringe-worthy method used in more than one paper to confirm Fe3+ binds to the sensor in aqueous solution, is mass spectroscopic detection of the ferric complex prepared in methanol. I have no doubt that they detected the complex, but Fe3+ in methanol is completely different than in water. The MS data in methanol does not confirm anything about the species that are (not) present in aqueous solution. 

What does one do in such a situation? Even if I was somehow asked to referee every paper on Fe3+ sensing, there were more papers on the topic published last year than I could possibly handle, even if they were the only kind of requests I received/accepted. A broad search suggests an upper limit of 190 Fe3+ sensor papers were published in 2014. I have no desire to comb the literature and complain to editors/authors every time I find a problematic paper. I've already published a paper in a good journal that includes a cautionary tale about these issues, but it does not seem to have permeated the sensing field zeitgeist. As I mentioned in the previous post, it's discouraging to find out that some individuals need a reminder about the relevant/underlying undergraduate inorganic chemistry. I have no doubt that researchers in other fields can point to similar problems in the literature on other topics. How does one effectively get through to journals, peer reviewers and researchers without wasting time that should be spent on other aspects of academic science? It seems antiquated in the information age that such mistakes should persist and be perpetuated, but the traditional practice of publishing an opposing research study is the only clear recourse.

Friday, March 20, 2015

Metal sensing malarkey: (or the expected virtue of ignorance)

To paraphrase Stephen Colbert, "who's not citing me now?" It's a refrain that many researchers can identify with, but only a small part of why I was motivated to write this post on peer review, journal policy and bad science. A little background first. A couple of months ago, I attended a research presentation that covered several papers on fluorescent sensors. My experience with fluorescent sensors dates back to the late 1990s and early 2000s when I completed my Ph.D. thesis on zinc probes with Stephen Lippard at MIT. At the time we started, fluorescent sensors for metal ions were still a niche area in inorganic/bioinorganic chemistry. Now, it's a widespread topic of research. As many realize, your Ph.D. work will follow (haunt) you long after graduation, even if you no longer actively work in that area. My group published a couple of papers on fluorescent probes for ferric iron 5 years ago, but that was the last time I actively worked in the area. Despite moving on to other topics of inquiry, I am still inundated with referee requests on fluorescent sensor papers, so I remain familiar with the progress and problems in the field.

The presentation focused on two papers published in ACS Applied Materials & Interfaces on fluoride and iron sensing respectively. I questioned the lead author giving the presentation about the validity of the methods and data interpretation, but failed to make any headway or get any concession that there may have been problems with the protocols or conclusions. So-called "post-publication peer review" has become rather controversial over the last few years as social media has facilitated the community's ability to discuss published science in an open forum. The scientific community becomes incensed in cases of fraud or plagiarism, although journals have often reacted more negatively to those who exposed the problems than to those responsible for the actual infractions. After consulting with several other experts on the underlying science and scientific publishing, I sent an email to the EIC of the journal detailing the problems with the papers. To be clear, I did not, and I am not making any accusation of misconduct.* Serious mistakes were made in the research that in part, or in whole invalidate the conclusions of the studies. Furthermore, it is troublesome that these issues were not addressed during the peer review process.

The EIC responded after several days promising to address each paper in a separate message. His response to the fluoride paper was the only course of action would be to submit a peer reviewed comment (providing this as an example) where the author would have a chance to respond, since the paper had been in print for nearly 2 years. I did not find this to be a particularly satisfying response since any publishable comment would need to be supported with new information. Essentially collecting the data and conducting control studies that should have been requested by peer reviewers. With the current state of knowledge, a potential published comment could be summarized as "I think you're wrong" and speculation, which is not any better than what was done in the paper. Data-free speculation does not not usually hold up to peer review, so reluctantly I published my criticism on pubpeer with the hope that anyone seeking to follow-up or use this chemistry would be wary of the authors' conclusions. This is the greatest risk in a case of erroneous research, which makes it similar to some issue encountered in cases of data falsification. Any time spent trying to use flawed science, wastes time and resources that could go toward more productive efforts. Coincidentally, I came across this paper today on fluoride sensing that invokes attack on a positively changed ring (albeit a different heterocycle), which was my initial instinct for an alternative mechanism in the disputed study. I'll have to compare the data and see if it gives me any new insight.

As for the iron paper, I never received the promised response. About 6 weeks after the initial inquiry, I wrote again asking for an update. After receiving nothing during the last +2 weeks, I am once again in the position of not having any particular recourse other than forgetting about it, or providing public post-publication peer review. Of the 2 papers, the iron sensor annoyed me more, because it repeats the same mistake made by another group that my group investigated and published as part of a larger study.

In a 2005 JACS article, Rurack claimed his Fe3+ responsive sensor also worked in aqueous solution. The only significant difference between the Rurack sensor and the new one is the receptor for the metal ion; however, both rely on the same PeT signal transduction mechanism where coordination to the aniline nitrogen atom is the key event. Several years after the Rurack paper was published, my group attempted to use the same receptor for a different application. We spent many months working on the system and eventually had to re-evaluate the Rurack data because our observations did not match what had been reported. We ultimately demonstrated that while Rurack's sensor did bind and respond to Fe3+ in organic solvents that lacked alcohol or carbonyl functional groups, the fluorescence signal in water was due to protonation of the aniline nitrogen atom, which mimics an Fe3+ response. We were fortunate to still be able to develop an interesting story even though we started our investigation with a flawed premise from a published paper (in JACS!). In a similar manner, the new Fe3+ sensor paper provides the opportunity to examine both pre- and post-publication peer review in this post.

The error the authors made in new paper is essentially the same  you absolutely cannot titrate Fe3+ into aqueous solution unless you use use a complexing ligand (e.g. citrate, which has a log K > 10 for Fe3+ and would therefore bind the metal ion more tightly than the sensor) or work at pH ≤ 3. In aqueous solution, Fe3+ rapidly hydrolyzes to Fe(OH)3 plus three equivalents of H+. The pKas for the 1st three deprotonation events are 2.2, 2.9 and ~6. This neglects multi-Fe processes that are also possible and have similarly acidic pKas. This is not an obscure fact, but textbook chemistry that would be covered in a standard undergraduate course. It's a fundamental concept in bioinorganic chemistry used to discuss the importance of siderophores in the acquisition of iron by microorganisms and the acquisition/transport/storage of iron by higher organisms using proteins.

The authors perform their fluorescence assays in 9:1 H2O-CH3CN. The water is not buffered and the authors do not report the pH at the beginning or the end of the fluorescence titration. A back of the envelope calculation shows that at ~150 equiv of Fe3+ added (~1000 μM Fe3+), the pH of the solution should reach ~3 (the approximate point at which Fe3+ hydrolysis no longer occurs and Fe3+ persists in solution). This is also the point at which the fluorescence response levels off for the sensor. The calculation is based on the use of deionized water without accounting for dissolved CO2, not that it would make a huge difference. CH3CN can act as a metal-binding ligand, but CH3CN does very little to stabilize Fe3+ in water. The authors go on to claim that reversibility of the fluorescence response with TPEN (tetrapyridylethylenediamine), a strong metal chelator, demonstrates that the fluorescence response is Fe3+-induced. This is also a flawed conclusion because the pKa of a protonated pyridine is about the same as a protonated aniline (both pKa ~ 5) and the aliphatic amines of TPEN are even more basic. Coordination (protonation) of the aniline nitrogen atom drives the PeT process responsible for the fluorescence response. TPEN can act as a base as well as a chelator, and the authors use a huge excesses of TPEN to demonstrate reversibility (60 equiv or 360 equiv of N bases). There may be some modest equilibrium between [Fe(Sensor)]3+ and [H(Sensor)]+ at pH<3, but the authors are observing a H+-, not an Fe3+-based fluorescence response in their titration. The argument is further supported by the receptor being used. Ethers are notoriously poor metal binding ligands in water. It would be very surprising if a cryptand ligand, even one with as many donor groups as the one in this sensor, could stable an Fe3+ complex with in water. The low affinity for the purported "[Fe(Sensor)]3+ complex" based on the fluorescence data supports this conclusion.

Returning to the Rurack report, the erroneous aqueous chemistry accounted for perhaps 25% of the discussion/conclusions in the paper. The rest of the Rurack paper is correctly interpreted (and an interesting counter-intuitive inorganic story). The flawed methodology accounts for 100% of the discussion/conclusions in the new paper. In my opinion this paper should be withdrawn; however, the EIC's lack of a response suggests that this isn't going to happen. I'd also like to contrast the response I got from the editor at Inorganic Chemistry to the one I got from ACS Applied Materials and Interfaces. Granted, I was trying to published a completed study in Inorg. Chem., but it should not be necessary to conduct months worth of work to prove something that only requires an understanding of basic inorganic chemistry. The Inorg. Chem. editor carefully handled the situation and facilitated a review of the conflicting data by the original author. I recall that I might have sent the EIC a note afterwards commending the editor who handled the situation. To his credit, Rurack completely supported the publication of our paper. The only unfortunate thing is that there is no indication anywhere that the original JACS paper contains a flawed set of experiments 
except in our paper. I still see this paper cited periodically as evidence that Fe3+ sensing can be done in aqueous solution. 

As an aside, our Inorg. Chem. paper was kind of an "end of the innocence" moment for me in scientific publishing. As a recent news story on pubpeer indicates, you can't always believe what you read in scientific journals. As someone who looks at sensor papers regularly, fluorescence might be the most misinterpreted spectroscopic assay used in chemistry. Fluorescence is an easy to execute and readily available technique, but there is a great tendency to interpret the results without acquiring additional supporting data (e.g. absorption spectroscopy, product analysis, etc.). As part of the Inorg. Chem. paper, my postdoc was trying to obtain a crystal structure of the Fe3+ complex of the ligand. After many failed attempts, he tried with Cu2+, and to our surprise got a structure containing only Cu1+. Another colleague in the fluorescent sensing field, pointed us in the direction of a synthetic paper where Cu2+ in CH3CN is used as a 1 electron oxidant (by forming [Cu(CH3CN)4]+). This was clearly what happened in our crystallization as we used CH3CN as the solvent. Despite our attempts to educate the fluorescent sensor community about the dangers of using Cu2+ in CH3CN, this is still a common practice. There are dozens of ring-opening spirolactam probes for Cu2+. These probes are usually based on rhodamine fluorophores, which have 2 embedded aniline groups, and give a terrific fluorescence response in CH3CN; however, everyone attributes the signal transduction mechanism to coordination/Lewis acidity of Cu2+, and ignores the possible contributions of redox chemistry.

There are clearly problems with peer review. In going through my significant backlog of TOC alerts today, I realized that RSC Advances moved to a 100 issues/year publishing schedule in 2014. This is a tremendous number of papers for a single journal, which requires a correspondingly huge number of peer reviewers. Inevitably, the same people who make mistakes in their research will be asked to review papers on similar science. This lets more errors slip through to publication and propagates errors in the literature. So what should editors do when they are alerted to a potentially serious problem? "Nothing" does not seem like an appropriate answer. Is pubpeer the the right pathway? It appears that some journals are very resistant to changing the status quo, and unless the pubpeer comments are linked to the articles, post-publication peer review may go unnoticed. It also remains to be seen if flawed protocols/conclusions will generate the kind of impassioned response that accompanies cases of scientific fraud; however, anyone who has wasted time with someone else's scientific mistakes surely has an opinion they will share without much prompting.

Update 3/22/15:
A note added in proof: the same group has a similar K+ sensor using a very similar receptor. The amides from the Fe3+ system are replaced by anilines, which would make metal interactions stronger. This sensor does not respond to Fe3+; however, the authors used buffered water, which means that protons from the are prevented from interacting with the aniline fluorescence switch. There is almost certainly an impact of having 3 "basic" aniline nitrogen atoms in the receptor as the amount of buffer (5 mM) is low compared to the added metal ions.

*The PI has since move to NJIT as a Dean, which would suggest the research group at UCF is no longer active. He is and was listed as a member of the editorial advisory board for ACS Applied Materials and Interfaces. While it is not uncommon and should not be problematic for board members to publish in the journal for which they serve, this may make some readers more suspicious about the impartiality of the peer review process.

Tuesday, January 6, 2015

Periodic table challenge

There was a phenomenal response to my blog post on the periodic table with emphasis graphic (thanks everyone!). While I still hope to uncover more information about the history of the graphic and gain insight into what Sheehan thought about it in his later years, I suspect that Sheehan was always aware that the relative sizes of the different element blocks did not accurately represent the abundance of the elements. For the target audience of pre-college (elementary?) students however, it no doubt succeeded fantastically in generating curiosity about the periodic table and stimulating interest in chemistry. As I hope was clear, my criticism was not directed at Sheehan's pedagogical efforts but rather at the indiscriminate spread of an inaccurate "meme" portrayed as a truism. The Sheehan periodic table appeals to both our aesthetic sensibilities as well as a human desire to simplify the complex. For the same reason it was an effective outreach tool, it became the perfect mechanism to propagate misinformation.

As several have pointed out, this will not be the last time Sheehan's graphic surfaces. We can point of the errors in the graphic every time that it is shared (maybe using my blog post), but a better approach would be to displace it from the zeitgeist. Since I lack the necessary artistic skills, I'm issuing a challenge for someone to create a periodic table that illustrates relative abundance. Sadly, I can't think if anything to offer as a reward, unless there is a sudden uptick in demand for signed reprints of my papers. 

As I cited in the original blog post, several versions of the periodic table showing abundance exist; however, each have shortcomings. The new periodic table with emphasis should meet the following criteria:

1. The periodic table must be visually striking. It should be more aesthetically appealing than Sheehan's graphic. It must encourage sharing and therefore promote education.

2. The periodic table must show all the naturally occurring elements (i.e. at least up to uranium, element 92). Obviously, this the hardest thing to achieve. As we've pointed out, the magnitude of the difference between most abundant and least abundant elements precludes presentation on anything resembling the standard periodic table. The weakness of the existing elemental abundance cartograms and the Google table is that one could conclude that rare elements do not exist. Using Google's periodic table as an example, it is accurate to say that astatine is present at 0 ppm in the Earth's crust, but it is incorrect to say astatine does not exist on earth. If one looked in locations with deposits of radioactive uranium and thorium ores, astatine would be detectable. Google also shows radon at 0 ppm. If radon was nonexistent on earth, radon abatement systems would be relegated to the dustbin of pseudoscience with the QRay bracelet and rhino horn. Radon can be found at approximately parts per trillion in the crust, but concentrated in uranium and thorium ore. 

While the cartograms pass criteria 1, Google's periodic table offers nothing beyond a standard visual. The same lack of artistry applies to all the other abundance tables that I have found.

To get people thinking, I have the skeleton of 2 possible ideas
A) An interactive periodic table that operates like Google Earth. A wide view would show the abundant elements, and the less abundant would come into view as the user zooms in closer. The big difference between Google Earth and this hypothetical periodic table is the amount of zoom required. The transition from a complete map of the continents down to the the standard street level map requires zooming through approximately 6 orders of magnitude. The abundance of elements is a much larger range of values (ca. >20 orders of magnitude).

B) A 2-fold Sheehan-inspired periodic table. The basis for this would be a color coded log scale. Colors would follow the electromagnetic spectrum such that each order of magnitude corresponds to a color (e.g. 10-16 abundance = violet with colors red shifting as the magnitude increases). Within a given color/order of magnitude, the blocks are sized relative to one another similar to Sheehan's graphic and cartograms.

To get you started, here's one possible resource for finding the amount of the elements in the crust or oceans.